Author response:

Reviewer #1 (Public Review):

The work of Umetani et al. monitors the death of about 100,000 cells caused by lethal antibiotic treatments in a microfluidic device. They observe that the surviving bacteria are either in a dormant or in a non-dormant state prior to the antibiotic treatment. They then study the relative abundances of these different persister cells when varying the physiological state of the culture. In agreement with previous observations, they observe that late stationary phase cultures harbor a high number of dormant persister cells and that this number goes down as the culture is more exponential but remains non-zero, suggesting that cultures at the exponential phase contain different types of persister bacteria. These results were qualitatively similar in a rich and poor medium. Further characterization of the growing persister bacteria shows that they often form Lforms, have low RpoS-mcherry expression levels and grow only slightly more slowly than the non-persister bacteria. Taken together, these results draw a detailed view of persister bacteria and the way they may survive extensive antibiotic treatments. However, in order to represent a substantial advance on previous knowledge, a deeper analysis of the persister bacteria should be done.

We thank the reviewer for suggesting the addition of more detailed analyses of persister cells. As we wrote in our response to Essential Revision 1, we now include a new section titled “Response of growing persisters to Amp exposure is heterogeneous” (Page 11-12) and present the results of the detailed analyses of single-cell dynamics of growth and cell morphology over the course of the pre-exposure, exposure, and post-exposure periods (Fig. 2D and H, Fig. 4B and D, Fig. 4 – figure supplement 1 and 2, Fig. 5B and D, Fig. 5 – figure supplement 1, Fig. 8B and D, and Figure 8 – figure supplement 1). The new results characterize differential responses to Amp treatment among growing persister cells (Fig. 4A-D, Fig. 4 – figure supplement 1, Fig. 4 – figure supplement 2A, Fig. 5A-D, and Fig. 5 – figure supplement 1), comparable division rates of MG1655 between non-surviving cells and persister cells growing prior to antibiotic treatments (Fig. 4E and Fig. 8E), except for the post-exponential phase cell populations of MF1 to Amp treatment in the LB medium and the post-exponential phase cell populations of MG1655 to Amp treatment in the M9 medium (Fig. 4 – figure supplement 2B and Fig. 5E) and the presence of persister cells to CPFX that avoid filamentation after the treatment (Fig. 8C and D, and Fig. 8 – figure supplement 1). We believe that these new analyses would provide new insights into the diverse dynamics and survival modes of antibiotic persistence at the single-cell level and represent important contributions to the field.

Reviewer #2 (Public Review):

The main question asked by Umenati et al. is whether persister cells to ampicillin arise preferentially from dormant, non-dividing cells or from cells that are actively growing before antibiotic exposure. The authors tracked persister cells generated from populations at different growth phases and culture media using a microfluidic device coupled to fluorescence microscopy, which is a challenge due to the low frequency of these persister cells. One of the main conclusions is that the majority of persisters arising in exponentially-growing populations originated from actively-dividing cells before the antibiotic treatment, reinforcing the idea that dormancy is not a prerequisite for persister formation. The authors made use of a fluorescent reporter monitoring RpoS activity (RpoS-mCherry fusion) and observed that RpoS levels in these persister cells were low. In the few lineages that exhibited no growth before the ampicillin treatment, RpoS levels were low as well, indicating that RpoS is not a predictive marker for persistence. By performing the same experiment with early and late stationary phase cultures, the authors observed that the proportion of persister cells that originated from dormant cells before the ampicillin treatment is significantly increased under these conditions. In the late stationary phase condition, dormant cells were expressing high levels of RpoS. The authors suggested that RpoS-mCherry proteins form aggregates which were suggested by the authors to be a characteristic of 'deep dormancy'. These cells were mostly unable to restart growth after the antibiotic removal while others with the lowest levels of RpoS tended to be persister. Confirming that these cells indeed contain protein aggregates as well as determining the physiological state of these cells appears to be crucial.

We thank reviewer #2 for pointing out the critical issue with the RpoS-mCherry fusion that we used to quantify RpoS expression levels in single cells in the original manuscript. As explained in our reply to the comments below, we performed a suggested experiment and confirmed that the RpoS function was impaired by tagging it with mCherry. To resolve this issue, we repeated almost all the experiments using the wild-type strain MG1655 and confirmed the reproducibility of the main results (Fig. 3, Fig. 3 – figure supplement 1, and Fig. 7). Due to this change of the main strain used in this study, we removed the results on the correlation between RpoS expression and the persistence trait in the revised manuscript because it may not reflect the relationship of intact RpoS. However, we decided to still keep and show some of the results with the MF1 strain, such as the population killing curves and the survival mode analyses, because they also provide insight into the role of RpoS in antibiotic persistence. In particular, we found both beneficial and detrimental effects of RpoS on antibiotic persistence, depending on culture conditions and duration of antibiotic treatment (Fig. 1 – figure supplement 3 and Fig. 6 – figure supplement 1). Therefore, we have included these results and related discussions in the revised manuscript.

Reviewer #3 (Public Review):

In their manuscript, Umetani, et al. address the question of the origin of persister bacteria using single-cell approaches. Persistence refers to a physiological state where bacteria are less sensitive to antibiotherapy, although they have not acquired a resistance mutation; importantly, the concept of persistence has been refined in the past decade to distinguish it from tolerance where bacteria are only transiently insensitive. Since persister cells are very rare in growing populations (typically 1e-5 or 1e-6), it is very challenging to observe them directly. It had been proposed that individual cells surviving antibiotics are not growing at the start of the treatment, but recent studies (nicely reviewed in the introduction) where persister bacteria were observed directly do not support this link. Following a similar line, the authors nonetheless still aim at "investigating whether non-growing cells are predominantly responsible for bacterial persistence". Based on new experimental data, they claim the contrary that most surviving cells were "actively growing before drug exposure" and that their work "reveals diverse survival pathways underlying antibiotic persistence".

We thank the reviewer for this helpful comment, which suggested to us that some revisions in our Introduction would better place our study in the context of previous understanding of antibiotic persistence. As mentioned in our response to Essential Revision 4 and the second comment of Reviewer 1's Recommendations for the authors, we have modified the Introduction to more appropriately place our study in the context of the field.

The main strengths of the manuscript are in my opinion:

- To report on direct observation of E. coli persisters to ampicillin (200µg/mL) in 5 different growth media (typically 20 persisters or more per condition, one condition with 12 only), which constitutes without a doubt an experimental tour de force.

- To aim at bridging the population level and the single-cell level by measuring relevant variables for each and analyzing them jointly.

- To demonstrate that in most conditions a large fraction of surviving cells was actively growing before drug exposure.

In addition, although it is well-known that E. coli doesn't need to maintain its rod shape for surviving and dividing, I found very remarkable in their data the extent to which morphology can be affected in persister cells and their progeny, since this really challenges our understanding of E. coli's "lifestyle" (these swimming amoeba-like cells in Supp Video 11 are mind-blowing!).

We are grateful to the reviewer for the articulation of the strength of this study. 

Unfortunately, these positive aspects are counter-balanced by several shortcomings in the way experiments are analyzed and interpreted, which I explain below. Moreover, the manuscript is written in a way that makes it very hard to find important information on how experiments are done and is likely to leave the reader with an impression of confusion about what the main findings actually are.

We thank the reviewer for pointing out these important issues regarding the original manuscript. Please see our replies below regarding how we corresponded to each specific comment to resolve the issue. To make the experimental methods and procedures more accessible and interpretable, we have added more explanations of the experimental details to the Results and Methods sections. Furthermore, since we understood that some of the confusions came from the insufficient explanation of the preculture procedures for the microfluidic experiments, we have modified the schematic illustration of the method shown in Fig. S1 in the original manuscript and moved it as the first main figure in the revised manuscript (Fig. 1C and D). We have also added an illustration that explains the cultivation procedures for the batch culture experiments as Fig.

6A. 

My major concerns are the following:

(1) The main interpretation framework proposed by the authors is to assess whether cells not growing before drug exposure (so-called "dormant") are more or less likely to survive the treatment than growing ones ("non-dormant"). Fig 2A and Fig 3G show the main conclusions of the article from this perspective, that growing cells can survive the treatment and that the fraction of persisters in a given condition is not explained by the fraction of "dormant" cells, respectively. With this analysis, the authors essentially assume that "dormant" cells are of the same type in their different conditions, which ignores the progress in this field over the last decade (Balaban et al. 2019). I argue on the contrary that the observation of "diverse modes of survival in antibiotic persistence" is expected from their experimental design. In particular, the sensitivity of E. coli to beta-lactams such as ampicillin is expected to be much lower during the lag out of the stationary phase, a phenomenon which has been coined "tolerance"; hence in the Late Stationary condition, two subpopulations coexist for which different response to ampicillin is expected. I propose steps toward a more compelling interpretation of the experimental data. Should this point be taken seriously by the authors, it, unfortunately, implies a major rewriting of the article, including its title.

We thank the reviewer for bringing to our attention the point that may have caused confusion in the original manuscript. 

The primary purpose of this manuscript was not to assess whether non-growing cells prior to drug exposure are more or less likely to survive treatment than growing cells. Rather, we wanted to examine how different persister cell dynamics emerge at the single-cell level depending on previous cultivation history, growth media, and antibiotic types. We believe that this point is clearer in the revised manuscript with the newly added single-cell dynamics data (Fig. 2D, 2H, 4B, 4D, Fig. 4 – figure supplement 1 and 2A, Fig. 5B, 5D, Fig. 5 – figure supplement 1, Fig. 8B, 8D, and Fig. 8 – figure supplement 1). 

We also did not mean to imply that "dormant cells" were of the same type under different conditions, as we were aware of the diversity of cellular states of non-growing cells, as well as the reduced sensitivity of cells to antibiotics during the lag out of stationary phase. We believe that one of the reasons this point may have been unclear is that in the previous version we had referred to all cells that were not growing prior to antibiotic treatment as "dormant cells", a term that is often used in a more restricted way to refer to cells under prolonged growth arrest. Therefore, in the revised manuscript, we have avoided the term "dormant cells" and instead simply referred to these as "non-growing cells". Accordingly, we have changed the title of the paper from "Observation of non-dormant persister cells reveals diverse modes of survival in antibiotic persistence" to "Observation of persister cell histories reveals diverse modes of survival in antibiotic persistence".

To further address these points, we have improved the description of the experimental procedures for the single-cell measurements (see the reviewer's next comment as well). The nongrowing persisters of the MF1 strain found in the post-exponential phase cell populations must be of a different type than those found in the post-early and post-late stationary phase cell populations due to the experimental design. All early and late stationary phase cells were maintained in a non-growing state by flowing conditioned media prepared from the early and late stationary phase cultures until the start of the time-lapse measurements. Thus, aside from potential physiological heterogeneity, the non-growing cells prior to drug treatment are all long lagging cells. On the other hand, for the post-exponential phase condition, we maintained exponential growth conditions during the period from the start of the second pre-culture to the start of antibiotic treatment, including the period during sample preparation for time-lapse measurements. Given the exponential dilution by growth of cell populations, the non-growing persisters are unlikely to be long lagging cells (see our response to Reviewer 2's third comment  in "Recommendations for the authors"). We now describe these experimental procedures in more detail in the Results section (L161-178, L287-297). In addition, we discuss the diversity of cellular states of both non-growing and growing cells in Discussion, citing literature (L545-557).

(2) The way the authors describe their experiments with bacteria in the stationary phase is very problematic. For instance, they write that they "sampled cells from early and late stationary phases (...) and exposed them to 200 μg/mL of Amp in both batch and single-cell cultures." For any reader in a hurry (hence skipping methods and/or supplementary figure), this leads to believe that bacteria sampled in the stationary phase were exposed to the drug right away (either by adding the drug to the stationary phase sample, or more classically by transferring cells to fresh media with antibiotics). However, it turns out that, after sampling and loading in the microfluidic device, bacteria are grown 2 h in LB (or 4 h in M9) - I don't know what to think of such a blatant omission. The names chosen for each condition should reflect their most important aspects, here "stationary" is simply not appropriate - maybe something like "post early stationary" instead. In any case, I believe that this point highlights further the misconception pointed out in 1 and implies that the average reader will be at best confused, and probably misled.

We again thank the reviewer for pointing out the insufficient explanation of the method for the single-cell measurements and the helpful recommendation regarding our nomenclature for different conditions. As mentioned above, we now present the previous supplementary figure that schematically explains the experimental procedure as the first main figure to clarify how we prepared the cells loaded into the microfluidic device for single-cell measurements (Fig. 1C and D). Also, following the reviewer's suggestion, we now refer to the conditions as "post-exponential phase," "post-early stationary phase," and "post-late stationary phase" in the revised manuscript. 

We included a 2-hour (or 4-hour in M9) cultivation period in fresh medium in batch cultures for measuring killing curves to make the cultivation conditions prior to antibiotic treatment as similar as possible between batch and microfluidic experiments. We have clarified the presence of preexposure cultivation of post-early stationary and post-late stationary phase cell populations in the fresh medium before treating them with antibiotics (L264-269, Fig. 6A), so that readers can more easily recognize the experimental conditions.

(3) Figures 4 and 5 are of very minor significance, and the methodology used in Fig 4 is questionable. The authors measure the abundance of an Rpos-mCherry translational fusion because its "high expression has been suggested to predict persistence". The rationale for this (that an RpoS-mCherry fusion would be a proxy for intracellular ppGpp levels, and in turn predict persistence) has never been firmly established, and the standards used in the article where this reporter was introduced (Maisonneuve, Castro-Camargo, and Gerdes 2013) are notoriously low (which eventually led to its retraction) - I don't know what to think of the fact that the authors cite a review by this group rather than their retracted article. While transcriptional fusions of promoters regulated by RpoS have been proposed to measure its regulatory activity (Patange et al. 2018), the combination of self-regulation and complex post-translational regulation of rpoS makes the physical meaning of the reporter used here completely unclear. Moreover, this translational fusion is introduced without doing any of the necessary controls to demonstrate that the activity of RpoS is not impaired by the addition of the fluorescent protein. Fig 5 simply reports the existence of persisters to ciprofloxacin growing before the treatment. This might be a new observation but it is not unexpected given that a similar observation has been made with a similar drug, ofloxacin (Goormaghtigh and van Melderen 2019), as pointed out in the introduction. There is no further quantitative claim on this.

We thank the reviewer for pointing out the issue of the RpoS-mCherry fusion. As we mentioned in our response to Essential Revision 2 and also to the comment from reviewer #2, we have tested the sensitivity of this fluorescent reporter strain to oxidative stress and confirmed that it is as sensitive as the rpoS strain (Fig. 1 – figure supplement 1C). Therefore, the RpoS function seems to be defective in this strain, as now explained in Results (L69-79). After confirming the problem with the RpoS-mCherry fusion, we removed all analyses and related arguments that relied on the RpoS expression level (previous Figure 4). In addition, we repeated almost all the experiments with the original MG1655 strain to confirm that the observed results are not specific to the problematic reporter strain. 

Regarding the experiments with CPFX, we have added a more detailed analysis of single cell dynamics and found that, contrary to the reported results for ofloxacin, not all persistent cells show filamentation after drug withdrawal (Fig. 8C and D, Fig. 8 – figure supplement 1). In addition, we performed new microfluidic experiments in which we treated post-late stationary phase cells with CPFX (Fig. 3). In contrast to the Amp treatment result and the previous study that reported the persistence of post-stationary phase cell populations to ofloxacin (ref. 20), all the persisters for which we identified the pre-exposure growth traits in this condition grew normally prior to CPFX treatment. These newly added analyses and experiments clarify the significance of the CPFX experiments. 

(4) The authors don't mention the dead volume nor the speed of media exchange in their device. Hopefully, it is short compared to the duration of the treatment; however, it is challenging to remove all antibiotics after the treatment and only 1e-3 or 1e-4 of the treatment concentration is already susceptible to affecting regrowth in fresh media. If this is described in another article, it would be worth adding a comment in the main text.

We thank the reviewer for bringing up this important point. We have added the perfusion chamber volume and medium flow rate information in the Methods section (L809-817).   

In the study in which two of the authors participated, the medium exchange rate across the semipermeable membrane was evaluated in a similar device with similar microchamber dimensions (ref. 26). There, we confirmed that the medium exchange was completed within 5 min, which is much shorter than the period of antibiotic treatment and post-antibiotic treatment periods for observing regrowth. We have also included this information in the main text with the reference (L58-63).

Despite the relatively high medium exchange rate, we cannot formally exclude the possibility that a small amount of antibiotic may remain in the device, e.g. due to non-specific adsorption on the internal surface of the microchambers. In such cases, the residual antibiotics may influence the physiological states of the cells and the regrowth kinetics in the post-exposure periods, as suggested by the reviewer. However, the frequencies of persister cells in the cell populations in our single-cell measurements are comparable to those in the batch culture measurements. Therefore, the removal of antibiotic drugs in our device is at least as efficient as in the batch culture assay. To clarify this point, we have added a paragraph to the Discussion with a reference that reviews the influence of antibiotics at concentrations significantly lower than the MICs (L482-

489).    

(5) Fig 2A supports the main finding that a significant fraction of bacteria surviving the treatment are growing before drug exposure, but it uses a poorly chosen representation.

- In order to compare between conditions, one would like to see the fraction of each type in the population.

- The current representation (of a fraction of each type among surviving cells) requires a side-byside comparison with a random sample (which will practically be equivalent to the fraction of each type among killed cells) in order to be informative.

We have changed the style of the previous Fig. 2A to show the fraction of each type in the population instead of the fraction of each type among surviving cells (Fig. 3 and Fig. 3-figure supplement 1).

Author response:

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

Reviewer #1 (Public review):

Weiler, Teichert, and Margrie systematically analyzed long-range cortical connectivity, using a retrograde viral tracing strategy to identify layer and region-specific cortical projections onto the primary visual, primary somatosensory, and primary motor cortices. Their analysis revealed several hundred thousand inputs into each region, with inputs originating from almost all cortical regions but dominated in number by connections within cortical sub-networks (e.g. anatomical modules). Generally, the relative areal distribution of contralateral inputs followed the distribution of corresponding ipsilateral inputs. The largest proportion of inputs originated from layer 6a cells, and this layer 6 dominance was more pronounced for contralateral than ipsilateral inputs, which suggests that these connections provide predominantly feedback inputs. The hierarchical organization of input regions was similar between ipsi- and contralateral regions, except for within-module connections, where ipsilateral connections were much more feed-forward than contralateral. These results contrast earlier studies which suggested that contralateral inputs only come from the same region (e.g. V1 to V1) and from L2/3 neurons. Thus, these results provide valuable data supporting a view of interhemispheric connectivity in which layer 6 neurons play an important role in providing modulatory feedback.

The conclusions of this paper are mostly well-supported by the data and analysis, but additional consideration of possible experimental biases is needed.

We thank the reviewer for their positive feedback on our manuscript.

Further discussion or analysis is needed about possible biases in uptake efficiency for different cell types. Is it possible that the nuclear retro-AAV has a tropism for layer 6 axons? Quantitative comparisons with results obtained with alternative methods such as rabies virus (Yao et al., 2023) or anterograde tracing (Harris et al., 2019) may be helpful for this.

We appreciate this technical comment. For the reasons indicated below we are confident that our AAV approach successfully and rather comprehensively labels inputs to the three target areas. Firstly, in the brains in which we injected our retrograde nuclear-AAV tracer into VISp, SSp-bfd or MOp we found several instances where layer 5 and/or layer 2/3 as was the dominant cortical projection layer (please see e.g. Figure 3 heatmaps). This was true for both ipsilateral and contralateral projection. 

Secondly, by way of comparison Yao et al., 2023 injected rabies virus into VISp (but not in SSp-bfd or MOp) and their results show notable similarities to ours: 1) They show that contralateral inputs to VISp (and higher visual areas) were mainly located in Layers 5 and 6. 2) Retrogradely labelled neurons in higher visual areas revealed anatomical hierarchy that reflects the known functional hierarchy of the mouse cortical visual system and that shown by our retro-AAV approach. Thus, as AAV and rabies based tracing lead to similar results, this is further evidence against bias via tropism of our AAV tracer. That said, direct comparisons of the results between our study and the Yao et al., 2023 study should be viewed with some caution since Yao et. al.  injected rabies virus into specific Cre-driver lines in which the rabies virus targets individual genetically defined cell types in specific layers. Importantly, because of the lack of a specific cre-driver line, L6 cortico-cortical (L6 CC) cells could not be targeted by their approach. Thus, the dataset in Yao et al., overlook the contribution of L6 CCs due to the lack of available Cre-lines. 

Thirdly, in a recent study (Weiler et al., 2024) we found that in a specific pathway (SSp-bfd→ VISp) both retro-AAV and the more traditional non-viral tracer cholera toxin subunit B (CTB) identified neurons in Layer 6 as the main source of projection neurons. The same results for the same pathway was shown by Bieler et al., 2019 (Bieler et al., 2017) using Fluorogold for retrograde tracing. Thus, the described dominance of Layer 6 projection neurons in specific pathways is likely not the result of a tropism of retro-AAV tracers. 

Please also see that we have now further extended the summary of these points in our revised manuscript in the discussion section (e.g. lines 457-463): 

Quantitative analysis of the injection sites should be included to account for possible biases. For example, L6 neurons are known to be the main target of contralateral inputs into the visual cortex (Yao et al., 2023). Thus, if the injections are biased towards or against layer 6 neurons, this may change the layer distribution of retrogradely labeled input cells. Comparison across biological replicates may help reveal sensitivity to particular characteristics of the injections.

In response to the reviewers' feedback, please see we have now quantified the injection volume per cortical layer, as shown in the revised Fig. S3D. Our results indicate that the injections were not biased toward Layer 6. Instead, the injected tracer volumes in Layers 1, 4, 5, and 6 were similar across all animals and injected areas. However, we observed that the injected tracer volume in Layer 2/3 tended to be higher than in other layers. Although the tracer volumes in Layers 2/3 appeared to be higher, the proportion of input neurons located in Layers 2/3 for most of the cortical projection areas was consistently lower than that from Layer 6. These findings provide strong evidence against injection bias towards L6 inputs.

The possibility of labelling axons of passage within the white matter should be addressed. This could potentially lead to false positive connections, contributing to the broad connectivity from most cortical regions that were observed.

For clarification, please see Fig.S2B in our revised manuscript. In this panel we plot the average percentage volume of the viral boli in the target areas and in all other nearby structures including the white matter. The percentage of virus injected into the white matter (WM) was 0.0824 ± 0.0759% for VISp and 0.0650 ± 0.0481 for SSp-bfd injections. Notably, injections into MOp showed no leakage into white matter (0%). These minimal volumes of virus in the white matter are unlikely to significantly influence the observed profile of widespread connectivity. Please see we have added a sentence to the Results section (lines 84-86) where we state that we only used brains that had a transduction of the white matter below 0.1%.

Reviewer #2 (Public review):

Summary:

Weiler et al use retrograde tracers, two-photon tomography, and automatic cell detection to provide a detailed quantitative description of the laminar and area sources of ipsi- and contralateral cortico-cortical inputs to two primary sensory areas and a primary motor area. They found considerable bilateral symmetry in the areas providing cortico-cortical inputs. However, although the same regions in both hemispheres tended to supply inputs, a larger proportion of inputs from contralateral areas originated from deeper layers (L5 and L6).

Strengths:

The study applies state-of-the-art anatomical methods, and the data is very effectively presented and carefully analyzed. The results provide many novel insights into the similarities and differences of inputs from the two hemispheres. While over the past decade there have been many studies quantitatively and comprehensively describing cortico-cortical connections, by directly comparing inputs from the ipsi and contralateral hemispheres, this study fills in an important gap in the field. It should be of great utility and an important reference for future studies on inter-hemispheric interactions.

We thank the reviewer for this encouraging feedback on our manuscript.

Weaknesses:

Overall, I do not find any major weakness in the analyses or their interpretation. However, one must keep in mind that the study only analyses inputs projecting to three areas. This is not an inherent flaw of the study; however, it warrants caution when extrapolating the results to callosal projections terminating in other areas. As inputs to two primary sensory areas and one is the primary motor cortex are studied, some of the conclusions could potentially be different for inputs terminating in high-order sensory and motor areas. Given that primary areas were injected, there are few instances of feedforward connections sampled in the ipsilateral hemisphere. The study finds that while ipsi-projections from the visual cortex to the barrel cortex are feedforward given its fILN values, those from the contralateral visual cortex are feedback instead. One is left to wonder whether this is due to the cross-modal nature of these particular inputs and whether the same rule (that contralateral inputs consistently exhibit feedback characteristics regardless of the hierarchical relationship of their ipsilateral counterparts with the target area,) would also apply to feedforward inputs within the same sensory cortices.

We acknowledge that what we find for primary sensory and motor target areas may not hold for other functionally different areas such as anterior cingulate cortex, retrosplenial cortex or frontal lobe that might be expected to receive strong feedforward cortical input. To begin to understand the organization of the global cortical input we have however first explored with primary sensory and motor areas. Please see that we have now added a sentence to the Discussion section of our manuscript that highlights the importance of investigating the hierarchical organization of intra and interhemispheric input onto higher cortical areas or within subregions of a given sensory area.

Another issue that is left unexplored is that, in the current analyses the barrel and primary visual cortex are analyzed as a uniform structure. It is well established that both the laminar sources of callosal inputs and their terminations differ in the monocular and binocular areas of the visual cortex (border with V2L). Similarly, callosal projections differ when terminating the border of S1 (a row of whiskers), and then in other parts of S1. Thus, some of the conclusions regarding the laminar sources of callosal inputs might depend on whether one is analyzing inputs terminating or originating in these border regions.

The aim of the present study was to analyse the global projectome to the VISp, SSp-bfd and MOp, irrespective of which subregions were included. Importantly, we purposely injected rather large bolus volumes to achieve large sample sizes of target neurons in each cortical layer.  For SSp-bfd, we utilised our previously reconstructed barrel map (Weiler et al., 2024) to precisely map our viral injection sites onto the barrels (Author response image 1). Analysis revealed that the six injection sites consistently encompassed 7–13 barrels (Author response image 1, three exemplary injection sites). Additionally, we determined the centres of mass for each injection site and mapped them onto the barrel map. Four of the injection sites were located in the lateral part of SSp-bfd, two in the central region, and none in the medial part. Notably, the injection sites within SSp-bfd exhibited significant overlap. As a result, a selective analysis of callosal projections targeting these injection sites would likely not yield distinct projection patterns, as the projectomes would inevitably include projections to surrounding barrels, leading to contamination.

Author response image 1.

Left: exemplary Injection sites mapped onto the 3D barrel map of SSp-bfd within the Mouse Allen Brain Atlas. Barrels were reconstructed using a specialized software as described previously (Weiler et al., 2024) Right: Centres of mass of all SSp-bfd injection sites mapped onto the 3D barrel map.

Due to the fact we covered a significant proportion of the respective target primary sensory area any further subdivision of these data is not possible and requires more tailored injections into clearly defined subareas. Investigating the separate projectomes onto these subregions (e.g. onto V1M and V1B) remains an important interesting research question that we, at least in part, will address in a future study.

Finally, while the paper emphasizes that projections from L6 "dominate" intra and contralateral cortico-cortical inputs, the data shows a more nuanced scenario. While it is true that the areas for which L6 neurons are the most common source of cortico-cortical projections are the most abundant, the picture becomes less clear when considering the number of neurons sending these connections. In fact, inputs from L2/3 and L5 combined are more abundant than those from L6 (Figure 3B), challenging the view that projections from L6 dominate ipsi- and contralateral projecting cortico-cortical inputs.

We agree in the case of the barrel cortex, layer 5 significantly contributes in terms of the number of brain areas projecting from within the ipsilateral and contralateral hemispheres. Please see we have replaced the term “dominates” in the title, abstract and in the manuscript where relevant.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

The sections analyzing the role of L6 towards feedback (pg. 11-13, Figure 6) were a bit verbose and confusing to me. Three possible models are proposed:

(1) a decrease in L23 projections, (2) an increase in L56 projections, or (3) both.

However, what is being quantified appears to be the fractions inputs, with L23. L5, and L6 summing to 1. Thus, a decrease in L23 would necessarily result in an increase in L56 projections. It seems like it would make more sense to quantify the percent change in the total number of inputs (rather than fractional) from each layer so that the 3 models are actually independent possibilities.

The issue with the suggested analysis is that, with one exception (one area projecting to MOp), the number of projection neurons in contralateral areas is always ~60-80% lower compared to their ipsilateral counterparts. Consequently, this is also true for the number of projection neurons in the different cortical layers. Thus, quantifying the percentage change from the ipsilateral to the contralateral hemisphere in the total number of inputs from each layer will always result in negative values. 

Nevertheless, we addressed the reviewer’s issue by calculating the preservation index (1(ipsi-contra)/(ipsi+contra)) for the sensory-motor areas independently for the absolute number of neurons within L2/3, 5 and 6 for the cortical areas projecting to VISp, SSp-bfd and MOp (see Author response image 2). When analysing the shift from the ipsilateral to the contralateral hemisphere, we observed that significantly more projection neurons were preserved in L6 compared to L2/3 for VISp and SSp-bfd. This shows that the number of L6 projection neurons declines less from the ipsilateral to the contralateral hemisphere compared to L2/3. However, our focus was on the fraction of projection neurons within each layer relative to the other layers per hemisphere (see Fig.6 of our manuscript). This measure is critical for distinguishing between feedforward and feedback connectivity. Calculating the change for each layer independently unfortunately does not provide insights into this comparison, as it does not capture the relative distribution of projection neurons across layers, which is central to our analysis. Therefore, we chose to present the data as layer fractions normalised within each hemisphere separately, enabling a comparison of relative changes between hemispheres, as shown in Fig.6 in the manuscript. We agree that with our approach a decrease in the fraction of L2/3 neurons would necessarily lead to an increase in the fraction of L5+6 neurons. However, as we analysed the fractional change for L5 and L6 separately, we found that the fraction of projection neurons in L5 generally showed only minor changes, while the fraction of L6 projection neurons increased substantially (Fig.6C). In addition, excluding L5 from the ipsi- or contralateral default network had significant effects on the fILN in only a relatively small number of projection areas. Excluding L6 resulted in significant changes in many more projection areas than layer 5.

Author response image 2.

Preservation index for L2/3, L5 and L6 of the 24 sensory-motor areas projecting onto the three target areas VISp, SSp-bfd and MOp.

Reviewer #2 (Recommendations for the authors):

I feel that there are a few conclusions that could be strengthened in the paper:

(1) The laminar sources of callosal inputs and their terminations differ in the monocular and binocular areas of the visual cortex (border with V2L. Similarly, callosal inputs are different close to the border of S1 with S2 than in the rest of the barrel cortex. From the methods sections and Figure S2, it seems that some injections targeted the V1 binocular zone while others were aimed at the monocular zone. Thus, it would be of interest to compare the laminar distribution and fILM of the contra inputs in inputs to the binocular and monocular zones (and S1 border vs the rest, if possible within this dataset).

Please see the answer for the reviewer’s second point in the public review (above).

(2) The results are currently a bit unclear on whether the contra inputs reflect the cortical hierarchy. Figure 4E-F makes it clear that the ipsi and contra fILMs do not always match. However, it seems from the plots in Figure 4D and Figure S6 that, while the contra fILM values are always higher, there might be a correlation between the ipsi and contra fILM. This could be addressed by directly plotting contra vs ipsi fILM.

Similarly, it would be useful to directly address if there is any hint of the visual hierarchy, as calculated in Figure S5 for the contra inputs.

Regarding the first point of the reviewer: We appreciate this comment. We do indeed find a positive correlation between the fILN ipsilateral and fILN contralateral across the individual cortical areas for all three targets. (please see Author response image 3 below). This is indeed an interesting observation that indicates a high degree of preservation concerning the rank order of the anatomical hierarchy within the input arising from both hemispheres. Please see we have included this new figure 4F into the manuscript and added a sentence in the results (lines 282-288): 

Regarding the second point of the reviewer: For visual hierarchy, although weaker, we find that the hierarchical ranking of the higher cortical visual areas is preserved for the contralateral hemisphere (see Author response image 3 below). 

Author response image 3.

Rank ordered average fILN values (± sem) of higher visual cortical areas of the ventral and dorsal visual stream for the ipsilateral and contralateral hemisphere.

(3) I find the emphasis in the title and other parts of the paper on Layer 6 corticocortical cells dominating the anatomical organization of intra and interhemispheric feedback a bit of an overstatement. While it is true that the areas for which L6 is the most abundant source of cortico-cortical projections are the most abundant (Figure 3C), when just focusing on the number of neurons sending corticocortical connections (Figure 3B), this is less clear. Ipsi connections are roughly divided 1/3, 1/3 , 1/3 between L2/3 , L5 and L6. In the contra, while projections from L6 neurons are the most abundant, there are not a majority and are less than those of L2/3 and L5 together. I suggest revising the statement about L6 cells dominating cortico-cortical connections to more accurately reflect these nuances.

(4) The observations from Figure 3 discussed above suggest that L6 inputs dominate in areas with less abundant projections to the injected areas. Is this the case? Is the fraction of L6 inputs inversely correlated with the number of inputs from that area?

Please see the following correlation plots for the total number of inputs versus the fraction of L6 inputs per area for both the ipsilateral and contralateral hemisphere. We do find on the ipsilateral hemisphere a negative correlation between the total number of inputs and the L6 input fraction for VISp and to a lesser degree for SSp-bfd. Interestingly, we find the opposite correlation for the ipsilateral MOp, contralateral VISp, SSp-bfd and MOp (Author response image 4, Author response table 1). While this is an interesting finding, the correlations often appeared to be weak and often absent within the individual animals and across the three target areas (Author response table 1). Thus, these correlations are seemingly not a general feature of cortical connectivity.

Author response image 4.

Total number of cells versus fraction of cells within L6 per cortical brain area (average across animals) for the ipsilateral (top) and contralateral (bottom) hemisphere for the three target areas VISp, SSp-bfd and MOp.

Author response table 1: Respective correlations between total numbers of cells and fraction of cells within L6 per cortical brain area for the ipsilateral and contralateral hemisphere for the three target areas (significant correlations highlighted with green).

Minor issues:

(5) Where was the mouse in Figure 3A injected?

In this exemplary mouse the retrograde tracer was injected into VISp. We added this information in the Figure legend of Figure 3A1. 

(6) Clarify in panel 4F that the position of the circle corresponds to the area location.

Done as suggested. 

References

Bieler M, Sieben K, Cichon N, Schildt S, Röder B, Hanganu-Opatz IL. 2017. Rate and Temporal Coding Convey Multisensory Information in Primary Sensory Cortices. eNeuro 4. doi:10.1523/ENEURO.0037-17.2017

Weiler S, Rahmati V, Isstas M, Wutke J, Stark AW, Franke C, Graf J, Geis C, Witte OW, Hübener M, Bolz J, Margrie TW, Holthoff K, Teichert M. 2024. A primary sensory cortical interareal feedforward inhibitory circuit for tacto-visual integration. Nat Commun 15:3081. doi:10.1038/s41467-024-47459-2

Yao S, Wang Q, Hirokawa KE, Ouellette B, Ahmed R, Bomben J, Brouner K, Casal L, Caldejon S, Cho A, Dotson NI, Daigle TL, Egdorf T, Enstrom R, Gary A, Gelfand E, Gorham M, Griffin F, Gu H, Hancock N, Howard R, Kuan L, Lambert S, Lee EK, Luviano J, Mace K, Maxwell M, Mortrud MT, Naeemi M, Nayan C, Ngo N-K, Nguyen T, North K, Ransford S, Ruiz A, Seid S, Swapp J, Taormina MJ, Wakeman W, Zhou T, Nicovich PR, Williford A, Potekhina L, McGraw M, Ng L, Groblewski PA, Tasic B, Mihalas S, Harris JA, Cetin A, Zeng H. 2023. A whole-brain monosynaptic input connectome to neuron classes in mouse visual cortex. Nat Neurosci 26:350–364. doi:10.1038/s41593-022-01219-x

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study aims to identify the proteins that compose the electrical synapse, which are much less understood than those of the chemical synapse. Identifying these proteins is important to understand how synaptogenesis and conductance are regulated in these synapses. The authors identified more than 50 new proteins and used immunoprecipitation and immunostaining to validate their interaction of localization. One new protein, a scaffolding protein, shows particularly strong evidence of being an integral component of the electrical synapse. However, many key experimental details are missing (e.g. mass spectrometry), making it difficult to assess the strength of the evidence.

Strengths:

One newly identified protein, SIPA1L3, has been validated both by immunoprecipitation and immunohistochemistry. The localization at the electrical synapse is very striking.<br /> A large number of candidate interacting proteins were validated with immunostaining in vivo or in vitro.

Weaknesses:

There is no systematic comparison between the zebrafish and mouse proteome. The claim that there is "a high degree of evolutionary conservation" was not substantiated.

We agree that we should have included a comprehensive comparison of proteins captured in the different species.  We are assembling this table and it will be included in the revised manuscript.  There is, indeed, significant conservation of many of the proteins enriched in both species.

No description of how mass spectrometry was done and what type of validation was done.

Since the mass spec was outsourced to a core facility, we had not included methodological details.  We have requested these and will include full details in the revised version of the manuscript.  In terms of “validation,” enrichment of proteins at electrical synapses was determined based on capture relative to control samples (non-transgenic zebrafish retinas or non-transgenic mouse retinas infected with the dGBP-TurboID virus) captured and processed at the same time.  Actual validations based on protein co-localization and pull-downs is the subject of the rest of the manuscript, and could only be done for a fraction of the identified proteins.  This type of validation can be pursued in many future studies. 

The threshold for enrichment seems arbitrary.

Yes, the thresholds are somewhat arbitrary.  This is due to the fact that experiments that captured larger total amounts of protein (mouse retina samples) had higher signal-to-noise ratio than those that captured smaller total amounts of protein (zebrafish retina).  This allowed us to use a more stringent threshold in the mouse dataset to focus on high probability captured proteins. 

Inconsistent nomenclature and punctuation usage.

We have scanned through the manuscript and updated terms that were used inconsistently in the interim revision of the manuscript.

To describe the mass spec procedure, we will get in touch with the mass spec facility and provide the details in the next round of submission.

The description of figures is very sparse and error-prone (e.g. Figure 6).

In Figure 1B, there is very broad non-specific labeling by avidin in zebrafish (In contrast to the more specific avidin binding in mice, Figure 2B). How are the authors certain that the enrichment is specific at the electrical synapse?

The enrichment of the proteins we identified is specific for electrical synapses because we compared the abundance of all candidates between Cx35b-V5-TurboID and wildtype retinas. Proteins that are components of electrical synapses, will only show up in the Cx35b-V5-TurboID condition. The western blot (Strep-HRP) in figure 1C shows the differences in the streptavidin labeling and hence the enrichment of proteins that are part of electrical synapses. Moreover, while the background appears to be quite abundant in sections, biotinylation is a rare posttranslational modification and mainly occurs in carboxylases: The two intense bands that show up above 50 and 75 kDa.  The background mainly originates from these two proteins.

In Figure 1E, there is very little colocalization between Cx35 and Cx34.7. More quantification is needed to show that it is indeed "frequently associated."

We agree that “frequently associated” is too strong as a statement. We corrected this and instead wrote “that Cx34.7 was only expressed in the outer plexiform layer (OPL) where it was associated with Cx35b at some gap junctions” in line 150. There are many gap junctions at which Cx35b is not colocalized with Cx34.7. 

Expression of GFP in HCs would potentially be an issue, since GFP is fused to Cx36 (regardless of whether HC expresses Cx36 endogenously) and V5-TurboID-dGBP can bind to GFP and biotinylate any adjacent protein.  

Thank you for this suggestion! There should be no Cx36-GFP expression in horizontal cells, which means that the nanobody cannot bind to anything in these cells. Moreover, to recognize specific signals from non-specific background, we included wild type retinas throughout the entire experiments. This condition controls for non-specific biotinylation.

Figure 7: the description does not match up with the figure regarding ZO-1 and ZO-2.

It appears that a portion of the figure legend was left out of the submitted version of the manuscript.  We have put the legend for panels A through C back into the manuscript in the interim revision.

Reviewer #2 (Public review):

Summary:

This study aimed to uncover the protein composition and evolutionary conservation of electrical synapses in retinal neurons. The authors employed two complementary BioID approaches: expressing a Cx35b-TurboID fusion protein in zebrafish photoreceptors and using GFP-directed TurboID in Cx36-EGFP-labeled mouse AII amacrine cells. They identified conserved ZO proteins and endocytosis components in both species, along with over 50 novel proteins related to adhesion, cytoskeleton remodeling, membrane trafficking, and chemical synapses. Through a series of validation studies¬-including immunohistochemistry, in vitro interaction assays, and immunoprecipitation - they demonstrate that novel scaffold protein SIPA1L3 interacts with both Cx36 and ZO proteins at electrical synapse. Furthermore, they identify and localize proteins ZO-1, ZO-2, CGN, SIPA1L3, Syt4, SJ2BP, and BAI1 at AII/cone bipolar cell gap junctions.

Strengths:

The study demonstrates several significant strengths in both experimental design and validation approaches. First, the dual-species approach provides valuable insights into the evolutionary conservation of electrical synapse components across vertebrates. Second, the authors compare two different TurboID strategies in mice and demonstrate that the HKamac promoter and GFP-directed approach can successfully target the electrical synapse proteome of mouse AII amacrine cells. Third, they employed multiple complementary validation approaches - including retinal section immunohistochemistry, in vitro interaction assays, and immunoprecipitation-providing evidence supporting the presence and interaction of these proteins at electrical synapses.

Weaknesses:

The conclusions of this paper are supported by data; however, some aspects of the quantitative proteomics analysis require clarification and more detailed documented. The differential threshold criteria (>3 log2 fold for mouse vs >1 log2 fold for zebrafish) will benefit from biological justification, particularly given the cross-species comparison. Additionally, providing details on the number of biological or technical replicates used in this study, along with analyses of how these replicates compare to each other, would strengthen the confidence in the identification of candidate proteins. Furthermore, including negative controls for the histological validation of proteins interacting with Cx36 could increase the reliability of the staining results.

While the study successfully characterized the presence of candidate proteins at the electrical synapses between AII amacrine cells and cone bipolar cells, it did not compare protein compositions between the different types of electrical synapses within the circuit. Given that AII amacrine cells form both homologous (AII-AII) and heterologous (AII-cone bipolar cell) electrical synapses-connections that serve distinct functional roles in retinal signaling processing-a comparative analysis of their molecular compositions could have provided important insights into synapse specificity.

Reviewer #3 (Public review):

Summary:

This study by Tetenborg S et al. identifies proteins that are physically closely associated with gap junctions in retinal neurons of mice and zebrafish using BioID, a technique that labels and isolates proteins proximal to a protein of interest. These proteins include scaffold proteins, adhesion molecules, chemical synapse proteins, components of the endocytic machinery, and cytoskeleton-associated proteins. Using a combination of genetic tools and meticulously executed immunostaining, the authors further verified the colocalizations of some of the identified proteins with connexin-positive gap junctions. The findings in this study highlight the complexity of gap junctions. Electrical synapses are abundant in the nervous system, yet their regulatory mechanisms are far less understood than those of chemical synapses. This work will provide valuable information for future studies aiming to elucidate the regulatory mechanisms essential for the function of neural circuits.

Strengths:

A key strength of this work is the identification of novel gap junction-associated proteins in AII amacrine cells and photoreceptors using BioID in combination with various genetic tools. The well-studied functions of gap junctions in these neurons will facilitate future research into the functions of the identified proteins in regulating electrical synapses.

Thank you for these comments.

Weaknesses:

I do not see major weaknesses in this paper. A minor point is that, although the immunostaining in this study is beautifully executed, the quantification to verify the colocalization of the identified proteins with gap junctions is missing. In particular, endocytosis component proteins are abundant in the IPL, making it unclear whether their colocalization with gap junction is above chance level (e.g. EPS15l1, HIP1R, SNAP91, ITSN in Figure 3B).

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors explore associations between plasma metabolites and glaucoma, a primary cause of irreversible vision loss worldwide. The study relies on measurements of 168 plasma metabolites in 4,658 glaucoma patients and 113,040 controls from the UK Biobank. The authors show that metabolites improve the prediction of glaucoma risk based on polygenic risk score (PRS) alone, albeit weakly. The authors also report a "metabolomic signature" that is associated with a reduced risk (or "resilience") for developing glaucoma among individuals in the highest PRS decile (reduction of risk by an estimated 29%). The authors highlight the protective effect of pyruvate, a product of glycolysis, for glaucoma development and show that this molecule mitigates elevated intraocular pressure and optic nerve damage in a mouse model of this disease.

Strengths:

This work provides additional evidence that glycolysis may play a role in the pathophysiology of glaucoma. Previous studies have demonstrated the existence of an inverse relationship between intraocular pressure and retinal pyruvate levels in animal models (Hader et al. 2020, PNAS 117(52)) and pyruvate supplementation is currently being explored for neuro-enhancement in patients with glaucoma (De Moraes et al. 2022, JAMA Ophthalmology 140(1)). The study design is rigorous and relies on validated, standard methods. Additional insights gained from a mouse model are valuable.

We thank the reviewer for these supportive comments.

Weaknesses:

Caution is warranted when examining and interpreting the results of this study. Among all participants (cases and controls) glaucoma status was self-reported, determined on the basis of ICD codes or previous glaucoma laser/surgical therapy. This is problematic as it is not uncommon for individuals in the highest PRS decile to have undiagnosed glaucoma (as shown in previous work by some of the authors of this article). The authors acknowledge a "relatively low glaucoma prevalence in the highest decile group" but do not explore how undiagnosed glaucoma may affect their results. This also applies to all controls selected for this study. The authors state that "50 to 70% of people affected [with glaucoma] remain undiagnosed". Therefore, the absence of self-reported glaucoma does not necessarily indicate that the disease is not present. Validation of the findings from this study in humans is, therefore, critical. This should ideally be performed in a well-characterized glaucoma cohort, in which case and control status has been assessed by qualified clinicians.

We appreciate the comment regarding the challenges of glaucoma ascertainment in UK Biobank. This is a valid limitation, as glaucoma in UK Biobank is based on self-reports and hospital records rather than comprehensive ophthalmologic examinations for all participants. To the best of our knowledge, there is no comparably sized dataset where all participants have undergone standardized glaucoma assessments, comprehensive metabolomic profiling, and high-throughput genotyping. Work is currently ongoing to link UK Biobank data to ophthalmic EMR data, which will help confirm self-reported diagnoses. This work is not complete, and the coverage of the cohort from such linkage is uncertain at present. Nonetheless, several factors speak to the validity of our findings. The top members of the metabolomic signature associated with resilience in the top decile of glaucoma polygenic risk score (PRS) decile—lactate (P=8.8E-12) and pyruvate (P=1.9E-10) —had robust values for statistical significance after appropriate adjustment for multiple comparisons, with additional validation for pyruvate in a human-relevant, glaucoma mouse model. Strikingly, the glaucoma odds ratio (OR) for subjects in the highest quartile of glaucoma PRS and metabolic risk score (MRS) was 25-fold, using participants in the lowest quartile of glaucoma PRS and MRS as the reference group. An effect size this large for a putative glaucoma determinant has only been seen for intraocular pressure (IOP), which is now largely accepted to be in the causal pathway of the disease.

The Discussion now contains the following statement: “A second limitation is that glaucoma ascertainment in the UK Biobank is based on self-reported diagnoses and hospital records rather than comprehensive ophthalmologic examinations. Nonetheless, it is reassuring that the prevalence of glaucoma in our sample (~4%) is similar to a directly performed disease burden estimate in a comparable, albeit slightly older, United Kingdom sample (2.7%)(79)”. (Lines 379-382)

The authors indicate that within the top decile of PRS participants with glaucoma are more likely to be of white ethnicity, while they are more likely to be of Black and Asian ethnicity if they are in the bottom half of PRS. Have the authors explored how sensitive their predictions are to ethnicity? Since their cohort is predominantly of European ancestry (85.8%), would it make sense to exclude other ethnicities to increase the homogeneity of the cohort and reduce the risk for confounders that may not be explicitly accounted for?

Comparing data in Tables 3 and 4 of the manuscript, we observe that, on a percentage basis, more individuals have glaucoma in the highest 10th percentile of risk compared to the lowest 50th percentile of risk across all ancestral groups.  We recently reported that the risk of glaucoma increases with each standard deviation increase in the glaucoma PRS across ancestral groups in the UK Biobank, utilizing a slightly different sample size (see Author response table 1 below). (1)Since the PRS is applicable across ancestral groups, we aim to make our results as generalizable as possible; therefore, we prefer to report our findings for all ethnic groups and not restrict our results to Europeans.

Author response table 1.

Performance of the mtGPRS Across Ancestral Groups in the UK Biobank

Abbreviations: mtGPRS, multitrait analysis of GWAS polygenic risk score; OR, odds ratio; CI, confidence interval.(1)

UK Biobank ancestry was genetically inferred based on principal component analysis. The OR represents the risk associated with each standard deviation change in mtGRS and is adjusted for multiple covariates including age, sex, and medical comorbidities.

In the discussion, we stated that “... we chose to analyze Europeans and non-Europeans together to make the results as generalizable as possible.” (Lines 378-379)

The authors discuss the importance of pyruvate, and lactate for retinal ganglion cell survival, along with that of several lipoproteins for neuroprotection. However, there is a distinction to be made between locally produced/available glycolysis end products and lipoproteins and those circulating in the blood. It may be useful to discuss this in the manuscript, and for the authors to explore if plasma metabolites may be linked to metabolism that takes place past the blood-retinal barrier.

As the reviewer points out, it is crucial to interpret the results for lipoproteins within the context of their access to the blood-retinal barrier. Even for smaller metabolites like pyruvate and lactate, it is essential to consider local production versus serum-derived molecules in mediating any neuroprotective effects. Our murine data suggest that exogenous pyruvate contributed to neuroprotection. However, for the other glycolysis-related metabolites (lactate and citrate), we cannot rule out the possibility that locally produced metabolites may also contribute to neuroprotection. None of the lipoproteins identified as potential resilience biomarkers had an adjusted P-value of less than 0.05. Nevertheless, HDL analytes can cross blood-ocular barriers to enter the aqueous humor.(2) Therefore, it is also possible for serum-derived HDL to influence retinal ganglion cell homeostasis. Overall, much more research is needed to clarify the roles of locally produced versus serum-derived factors in conferring resilience to genetic predisposition to glaucoma.

We have added the following sentences to the discussion:

“Notably, although our validation data confirm the neuroprotective effects of exogenous pyruvate, it remains possible that endogenously produced pyruvate within ocular tissues may also contribute to RGC protection.” (Lines 329-331)

“Furthermore, as HDL analytes can cross blood-ocular barriers,(78) there is a plausible route for serum-derived HDL to influence RGC homeostasis. Nonetheless, the relative contributions of circulating lipoproteins versus local synthesis within ocular tissues remain unclear and warrant further investigation.” (Lines 355-358)

“Incorporating ocular physiology and blood-retinal barrier considerations when interpreting lipoproteins as potential resilience biomarkers will be critical for future studies aimed at understanding and therapeutically targeting increased glaucoma risk.” (Lines 360-363)

Reviewer #2 (Public review):

Summary

The authors have used the UK Biobank data to interrogate the association between plasma metabolites and glaucoma.

(1) They initially assessed plasma metabolites as predictors of glaucoma: The addition of NMR-derived metabolomic data to existing models containing clinical and genetic data was marginal.

(2) They then determined whether certain metabolites might protect against glaucoma in individuals at high genetic risk: Certain molecules in bioenergetic pathways (lactate, pyruvate, and citrate) conferred protection.

(3) They provide support for protection conferred by pyruvate in a murine model.

Strengths

(1) The huge sample size supports a powerful statistical analysis and the opportunity for the inclusion of multiple covariates and interactions without overfitting the models.

(2) The authors have constructed a robust methodology and statistical design.

(3) The manuscript is well written, and the study is logically presented.

(4) The figures are of good quality.

(5) Broadly, the conclusions are justified by the findings.

We thank the reviewer for these supportive comments.

Weaknesses

(1) Although it is an invaluable treasure trove of data, selection bias and self-reporting are inescapable problems when using the UK Biobank data for glaucoma research. The high-impact glaucoma-related GWAS publications (references 26 and 27) referenced in support of the method suffer the same limitations. This doesn't negate the conclusions but must be taken into consideration. The authors might note that it is somewhat reassuring that the proportion of glaucoma cases (4%) is close to what would be expected in a population-based study of 40-69-year-olds of predominantly white ethnicity.

While there are limitations when open-angle glaucoma (OAG) is ascertained by self-report, as discussed above, we agree with the reviewer that the prevalence of glaucoma is consistent with data from population-based studies of Europeans who are 40-69 years of age. 

We also want to point out that references 26 and 27 indicate glaucoma self-reports can be an acceptable surrogate for OAG that is ascertained by clinical evaluation. Consider the methodologic details for each study:

Reference 26 is a 4-stage genome-wide meta-analysis to identify loci for OAG from 21 independent populations. The phenotypic definition of OAG was based on clinical assessment in the discovery stage, and 7286 glaucoma self-reports from the UK Biobank served as an effective replication set.  It is also important to note that 120 out of the 127 discovered OAG loci were nominally replicated in 23andMe, where glaucoma was ascertained entirely by self-report.

Reference 27 is a genome-wide meta-analysis to identify IOP genetic loci, an important endophenotype for OAG. The study identified 112 loci for IOP. These loci were incorporated into a glaucoma prediction model in the NEIGHBORHOOD study and the UK Biobank. The area under the receiver operator curve was 0.76 and 0.74, respectively, in these studies. While the AUCs were similar, OAG was ascertained clinically in NEIGHBORHOOD and largely by self-report in UK Biobank. 

Finally, a strength of the UK Biobank is that selection bias is minimized. Patients need not be insured or aligned to the study for any reason aside from being a UK resident. There is indeed a healthy bias in the UK Biobank. Ambulatory patients who tend to be health conscious and willing to donate their time and provide biological specimens tend to participate. We agree with the reviewer that the use of self-reported cases does not negate the conclusions, and hopefully, future iterations of the UK Biobank where clinical validation of self-reports are performed will confirm these findings, which already have some validation in a preclinical glaucoma model.

We add the following sentence to the first action item above regarding our case ascertainment method. “Nonetheless, it is reassuring that the prevalence of glaucoma in our sample (~4%) is similar to a directly performed disease burden estimate in a comparable, albeit slightly older, United Kingdom sample (2.7%)..”(3) (Lines 381-383)

(2) As noted by the authors, a limitation is the predominantly white ethnicity profile that comprises the UK Biobank. 

(3) Also as noted by the authors, the study is cross-sectional and is limited by the "correlation does not imply causation" issue.

While the epidemiological arm of our study was cross-sectional, the studies testing the ability of pyruvate to mitigate the glaucoma phenotype in mice with the Lmxb1 mutation were prospective.

We already pointed out in the discussion that pyruvate supplementation reduced glaucoma incidence in a human-relevant genetic mouse model.

(4) The optimal collection, transport, and processing of the samples for NMR metabolite analysis is critical for accurate results. Strict policies were in place for these procedures, but deviations from protocol remain an unknown influence on the data.

Comments 4 and 5 are related and will be addressed after comment 5.

(5) In addition, all UK Biobank blood samples had unintended dilution during the initial sample storage process at UK Biobank facilities. (Julkunen, H. et al. Atlas of plasma NMR biomarkers for health and disease in 118,461 individuals from the UK Biobank. Nat Commun 14, 604 (2023) Samples from aliquot 3, used for the NMR measurements, suffered from 5-10% dilution. (Allen, Naomi E., et al. Wellcome Open Research 5 (2021): 222.) Julkunen et al. report that "The dilution is believed to come from mixing of participant samples with water due to seals that failed to hold a system vacuum in the automated liquid handling systems. While this issue is likely to have an impact on some of the absolute biomarker concentration values, it is expected to have limited impact on most epidemiological analyses."

We thank the reviewer for making us aware of the unintended sample dilution issue from aliquot 3, used for NMR metabolomics in UK Biobank participants. While ~98% of samples experienced a 5-10% dilution, this would not affect our reported results, which did not rely on absolute biomarker concentrations. All metabolites in the main tables were probit transformed and used as continuous variables per 1 standard deviation increase.  Nonetheless, in supplemental material, we show the unadjusted median levels of pyruvate (in mmol/L) were higher in participants without glaucoma vs those with glaucoma, both in the population overall and in those in the top 10 percentile of glaucoma risk. 

Furthermore, we see no evidence in the literature that unidentified protocol deviations might impact metabolite results in UK Biobank participants. For example, a recent study evaluated the relationship between a weighted triglyceride-raising polygenic score (TG.PS) and type 3 hyperlipidemia (T3HL) in the Oxford Biobank (OBB) and the UK Biobank. In both biobanks, metabolomics was performed on the Nightingale NMR platform. A one standard deviation increase in TG.PS was associated with a 13% and 15.2% increased risk of T3HL in the OBB and UK Biobank, respectively.(4) Replication of the OBB result in the UK Biobank suggests there are no additional concerns regarding the processing of the UK Biobank for NMR metabolomics. Of course, we remain vigilant for protocol deviations that might call our results into question and will seek to validate our findings in other biobanks in future research.

Impact

The findings advance personalized prognostics for glaucoma that combine metabolomic and genetic data. In addition, the protective effect of certain metabolites influences further research on novel therapeutic strategies.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Given the uncertainty in the proportion of controls with undiagnosed glaucoma, it may be appropriate to include a sensitivity analysis in the manuscript. The authors could then provide the readers with an estimate of how sensitive their predictions are to the proportion of undiagnosed individuals among controls.

Since UK Biobank participants did not undergo standardized clinical assessments, it is not possible to perform sensitivity analyses as we don’t know which controls might have glaucoma, although we can offer the following comments.

We are performing a cross-sectional, prospective, detailed glaucoma assessment of participants in the top and bottom 10 percent of genetic predisposition recruited from BioMe at Icahn School of Medicine at Mount Sinai and Mass General Brigham Biobank at Harvard Medical School. We find that 21% of people in the top decile of genetic risk have glaucoma,(5) which compares reasonably well to the 15% of people in the top 10% of genetic risk in the UK Biobank. This underscores the assertion that our definition of glaucoma in the UK Biobank, while not ideal, is a reasonable surrogate for a detailed clinical assessment.

Currently, 10,077 subjects in the top decile of glaucoma genetic predisposition did not meet our definition of glaucoma. If we assume that the glaucoma prevalence is 3% and 50% of people with glaucoma are undiagnosed, then that would translate to an additional 150 cases misclassified as controls, which could either drive our result to the null, have no impact on our current result or contribute to a false positive result, depending on their pyruvate (and other metabolite) levels.   

We have already addressed the issue of a lack of standardized exams in the UK Biobank and the need for more studies to confirm our findings.

Reviewer #2 (Recommendations for the authors):

(1) I am curious about the proposed reason for some individuals having metabolic profiles conferring resilience. Plasma pyruvate levels are normally distributed. Is it simply the case that some individuals with naturally high levels of pyruvate are fortuitously protected against glaucoma? Some sort of self-regulation mechanism seems unlikely.

Thank you for your insightful question regarding the potential mechanism underlying the association between pyruvate levels and glaucoma resilience. There may be modest inter-individual differences which can have significant physiological implications, particularly in the context of neurodegeneration and metabolic stress. One possibility is that individuals with naturally higher pyruvate levels may benefit from pyruvate's known neuroprotective and metabolic support functions(6–8), which could confer resilience against the oxidative and bioenergetic challenges associated with glaucoma. Pyruvate is important for cellular metabolism, redox balance, and mitochondrial function - processes that are increasingly implicated in glaucomatous neurodegeneration. (9)Elevated pyruvate levels support mitochondrial ATP production(10), buffer oxidative stress,(11) and impact metabolic flux(12,13) through pathways such as the tricarboxylic acid cycle and NAD+/NADH homeostasis. This is consistent with prior studies suggesting that mitochondrial dysfunction contributes to retinal ganglion cell vulnerability in glaucoma.(14–17) While a direct self-regulation mechanism may seem unlikely, both genetic and environmental factors can influence pyruvate metabolism, which could lead to subtle but clinically meaningful variations in its levels. Our findings are supported by validation in a mouse model, which suggests that the association is less likely fortuitous, but there may be an underlying biological process that merits further mechanistic investigation. Future studies incorporating longitudinal metabolic profiling and functional validation in human-derived models will help better understand this relationship.

(2) Conceivably, the higher levels of pyruvate and lactate may have resulted from recent exercise and may reflect individuals with high levels of exercise that confers resilience against glaucoma by independent mechanisms such as improved blood flow. Any way to rule that out from the UK Biobank data?

Thank you for raising this important point. To account for the potential confounding effects of physical activity, we adjusted for metabolic equivalents of task (METs) in our models, a standardized measure of physical activity available in the UK Biobank. By incorporating METs as a covariate, we aimed to minimize the influence of individual exercise levels on plasma pyruvate and lactate levels. This helps us ascertain that the observed associations are not solely attributable to differences in physical activity. However, we do acknowledge that longitudinal analysis of exercise patterns would provide further clarity on this relationship. 

(3) It may be worth mentioning that the retinal ganglion cells contain a plasma membrane monocarboxylate transporter that supports pyruvate and lactate uptake from the extracellular space.

Thank you for this extremely insightful suggestion on retinal ganglion cell (RGC) expression of monocarboxylate transporters, which can facilitate the uptake of pyruvate and lactate from the extracellular space. This is relevant for our study, given the high metabolic demands of RGCs and their reliance on both glycolytic and oxidative metabolism for neuroprotection and survival.

We acknowledged this in the discussion section of the manuscript by adding the following statement: "RGCs express monocarboxylate transporters, which facilitate the uptake of extracellular pyruvate and lactate, improving energy homeostasis, neuronal metabolism, and survival.” (Lines 309-311)

(4) The mechanism of protection in the mice, at least in part, is likely due to the lower IOP in the pyruvate-treated animals. Did the authors investigate the influence of pyruvate on IOP in the UK Biobank data (about 110,000 individuals had IOP measurements)?

Thank you for your suggested investigation. We ran the suggested analysis among 68,761 individuals with IOP measurements and metabolomic profiling. Imputed pretreatment IOP values for participants using ocular hypotensive agents were calculated by dividing the measured IOP by 0.7, based on the mean IOP.

We plotted the relationship between IOP and pyruvate levels (probit transformed). We compared participants with pyruvate levels +2 standard deviations, above the mean (red dashed line), which has a probit-transformed value of 2 and an absolute concentration of 0.15 mmol/L. We found a statistically significant difference between the groups (p=0.017) using the Welch two-sample t-test. We have not added this analysis to the manuscript, but readers can find the data here as the reviews are public. We acknowledge and addressed the dilutional issue above, where we utilized probit-transformed metabolite levels analyzed as continuous variables per 1 SD increase, rather than absolute concentrations.

Author response image 1.

(5) Line 88: I suggest changing "patients" to "affected individuals". The term "patients" tends to imply that the individual has already been diagnosed, but the idea being conveyed is about underdiagnosis in the population.

Thank you for your suggestion.

We have added the change from "patients" to "affected individuals" in the introduction. (Line 90)

(6) Line 93: "However, glaucoma is also significantly affected by environmental and lifestyle factors,10-14". Although lifestyle risk factors such as caffeine intake, alcohol, smoking, and air pollution have been reported, the associations are generally weak and inconsistently reported. Consider modifying this notion to stress the emerging evidence around gene-environment interactions (reference 14) rather than environmental factors per se, with the implication that genes + metabolism may be greater than the sum of the parts.

Thank you for this thoughtful suggestion to highlight gene-environment interactions, where genetic susceptibility may amplify or mitigate the impact of metabolic and environmental influences on glaucoma progression. We have revised the statement to better reflect the synergistic effects of genetics and metabolism rather than considering environmental factors in isolation.

Revised sentence for inclusion in the introduction of the manuscript: "Glaucoma risk is influenced by both genetic and metabolic factors, with emerging evidence suggesting that gene-environment interactions may play a greater role in conferring disease risk than independent exposures alone.” (Lines 95-97)

(7) Lines 156-161: In model 4, rather than stating that the very small increase in AUC with the addition of metabolic data compared to clinical and genetic data alone, "modestly enhances the prediction of glaucoma", it may be better interpreted as a marginal difference that was statistically significant due to the very large sample size but not clinically significant.

Thank you for your suggested comment.

We have adjusted the wording by changing “modestly” to “marginally” to address that the statistical significance is in the context of the study’s large sample size in the results section (Line 162) and throughout the manuscript.

NB: We made other minor edits to correct minor grammatical errors, improve clarity, and streamline the revised manuscript. Furthermore, the paragraph regarding slit lamp examination in the Methods was inadvertently omitted but is added back in the revised manuscript (Lines 571-579).

References:

(1) Kim J, Kang JH, Wiggs JL, et al. Does Age Modify the Relation Between Genetic Predisposition to Glaucoma and Various Glaucoma Traits in the UK Biobank? Invest Ophthalmol Vis Sci. 2025;66(2):57. doi:10.1167/iovs.66.2.57

(2) Cenedella RJ. Lipoproteins and lipids in cow and human aqueous humor. Biochim Biophys Acta BBA - Lipids Lipid Metab. 1984;793(3):448-454. doi:10.1016/0005-2760(84)90262-5

(3) Minassian DC, Reidy A, Coffey M, Minassian A. Utility of predictive equations for estimating the prevalence and incidence of primary open angle glaucoma in the UK. Br J Ophthalmol. 2000;84(10):1159-1161. doi:10.1136/bjo.84.10.1159

(4) Pieri K, Trichia E, Neville MJ, et al. Polygenic risk in Type III hyperlipidaemia and risk of cardiovascular disease: An epidemiological study in UK Biobank and Oxford Biobank. Int J Cardiol. 2023;373:72-78. doi:10.1016/j.ijcard.2022.11.024

(5) Zhao H, Pasquale LR, Zebardast N, et al. Screening by glaucoma polygenic risk score to identify primary open-angle glaucoma in two biobanks: An updated report. ARVO 2025 meeting. Published online 2025.

(6) Zilberter Y, Gubkina O, Ivanov AI. A unique array of neuroprotective effects of pyruvate in neuropathology. Front Neurosci. 2015;9. doi:10.3389/fnins.2015.00017

(7) Quansah E, Peelaerts W, Langston JW, Simon DK, Colca J, Brundin P. Targeting energy metabolism via the mitochondrial pyruvate carrier as a novel approach to attenuate neurodegeneration. Mol Neurodegener. 2018;13(1):28. doi:10.1186/s13024-018-0260-x

(8) Gray LR, Tompkins SC, Taylor EB. Regulation of pyruvate metabolism and human disease. Cell Mol Life Sci. 2014;71(14):2577-2604. doi:10.1007/s00018-013-1539-2

(9) Harder JM, Guymer C, Wood JPM, et al. Disturbed glucose and pyruvate metabolism in glaucoma with neuroprotection by pyruvate or rapamycin. Proc Natl Acad Sci. 2020;117(52):33619-33627. doi:10.1073/pnas.2014213117

(10) Kim MJ, Lee H, Chanda D, et al. The Role of Pyruvate Metabolism in Mitochondrial Quality Control and Inflammation. Mol Cells. 2023;46(5):259-267. doi:10.14348/molcells.2023.2128

(11) Wang X, Perez E, Liu R, Yan LJ, Mallet RT, Yang SH. Pyruvate Protects Mitochondria from Oxidative Stress in Human Neuroblastoma SK-N-SH Cells. Brain Res. 2007;1132(1):1-9. doi:10.1016/j.brainres.2006.11.032

(12) Tilton WM, Seaman C, Carriero D, Piomelli S. Regulation of glycolysis in the erythrocyte: role of the lactate/pyruvate and NAD/NADH ratios. J Lab Clin Med. 1991;118(2):146-152.

(13) Li X, Yang Y, Zhang B, et al. Lactate metabolism in human health and disease. Signal Transduct Target Ther. 2022;7(1):305. doi:10.1038/s41392-022-01151-3

(14) Zhang ZQ, Xie Z, Chen SY, Zhang X. Mitochondrial dysfunction in glaucomatous degeneration. Int J Ophthalmol. 2023;16(5):811-823. doi:10.18240/ijo.2023.05.20

(15) Ju WK, Perkins GA, Kim KY, Bastola T, Choi WY, Choi SH. Glaucomatous optic neuropathy: Mitochondrial dynamics, dysfunction and protection in retinal ganglion cells. Prog Retin Eye Res. 2023;95:101136. doi:10.1016/j.preteyeres.2022.101136

(16) Jassim AH, Inman DM, Mitchell CH. Crosstalk Between Dysfunctional Mitochondria and Inflammation in Glaucomatous Neurodegeneration. Front Pharmacol. 2021;12. doi:10.3389/fphar.2021.699623

(17) Yang TH, Kang EYC, Lin PH, et al. Mitochondria in Retinal Ganglion Cells: Unraveling the Metabolic Nexus and Oxidative Stress. Int J Mol Sci. 2024;25(16):8626. doi:10.3390/ijms25168626

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

By way of background, the Jiang lab has previously shown that loss of the type II BMP receptor Punt (Put) from intestinal progenitors (ISCs and EBs) caused them to differentiate into EBs, with a concomitant loss of ISCs (Tian and Jiang, eLife 2014). The mechanism by which this occurs was activation of Notch in Put-deficient progenitors. How Notch was upregulated in Put-deficient ISCs was not established in this prior work. In the current study, the authors test whether a very low level of Dl was responsible. But co-depletion of Dl and Put led to a similar phenotype as depletion of Put alone. This result suggested that Dl was not the mechanism. They next investigate genetic interactions between BMP signaling and Numb, an inhibitor of Notch signaling. Prior work from Bardin, Schweisguth and other labs has shown that Numb is not required for ISC self-renewal. However the authors wanted to know whether loss of both the BMP signal transducer Mad and Numb would cause ISC loss. This result was observed for RNAi depletion from progenitors and for mad, numb double mutant clones. Of note, ISC loss was observed in 40% of mad, numb double mutant clones, whereas 60% of these clones had an ISC. They then employed a two-color tracing system called RGT to look at the outcome of ISC divisions (asymmetric (ISC/EB) or symmetric (ISC/ISC or EB/EB)). Control clones had 69%, 15% and 16%, respectively, whereas mad, numb double mutant clones had much lower ISC/ISC (11%) and much higher EB/EB (37%). They conclude that loss of Numb in moderate BMP loss of function mutants increased symmetric differentiation which lead caused ISC loss. They also reported that numb¹⁵ and numb⁴ clones had a moderate but significant increase in ISC-lacking clones compared to control clones, supporting the model that Numb plays a role in ISC maintenance. Finally, they investigated the relevance of these observation during regeneration. After bleomycin treatment, there was a significant increase in ISC-lacking clones and a significant decrease in clone size in numb⁴ and numb¹⁵ clones compared to control clones. Because bleomycin treatment has been shown to cause variation in BMP ligand production, the authors interpret the numb clone under bleomycin results as demonstrating an essential role of Numb in ISC maintenance during regeneration.

Strengths:

(i) Most data is quantified with statistical analysis

(ii) Experiments have appropriate controls and large numbers of samples

(iii) Results demonstrate an important role of Numb in maintaining ISC number during regeneration and a genetic interaction between Mad and Numb during homeostasis.

Weaknesses:

(i) No quantification for Fig. 1

Quantification of Fig.1 has been added. 

(ii) The premise is a bit unclear. Under homeostasis, strong loss of BMP (Put) leads to loss of ISCs, presumably regardless of Numb level (which was not tested). But moderate loss of BMP (Mad) does not show ISC loss unless Numb is also reduced. I am confused as to why numb does not play a role in Put mutants. Did the authors test whether concomitant loss of Put and Numb leads to even more ISC loss than Put-mutation alone.

We have tested the genetic interaction between put and numb using Put RNAi and Numb RNAi driven by esg^ts. According to the results in this study and our previously published data, put mutant clone or esg^ts > Put-RNAi induced a rapid loss of ISC (whin 8 days). We did not observe further enhancement of stem cell loss phenotype in Put and Numb double RNAi guts.

(iii) I think that the use of the word "essential" is a bit strong here. Numb plays an important role but in either during homeostasis or regeneration, most numb clones or mad, numb double mutant clones still have ISCs. Therefore, I think that the authors should temper their language about the role of Numb in ISC maintenance.

We have revised the language and changed “essential” to important”.

Reviewer #2 (Public review):

Summary:

This work assesses the genetic interaction between the Bmp signaling pathway and the factor Numb, which can inhibit Notch signalling. It follows up on the previous studies of the group (Tian, Elife, 2014; Tian, PNAS, 2014) regarding BMP signaling in controlling stem cell fate decision as well as on the work of another group (Sallé, EMBO, 2017) that investigated the function of Numb on enteroendocrine fate in the midgut. This is an important study providing evidence of a Numb-mediated back up mechanism for stem cell maintenance.

Strengths:

(1) Experiments are consistent with these previous publications while also extending our understanding of how Numb functions in the ISC.

(2) Provides an interesting model of a "back up" protection mechanism for ISC maintenance.

Weaknesses:

(1) Aspects of the experiments could be better controlled or annotated:

(a) As they "randomly chose" the regions analyzed, it would be better to have all from a defined region (R4 or R2, for example) or to at least note the region as there are important regional differences for some aspects of midgut biology.

Thank you for the suggestion. In fact, we conducted all the analyses in region 4, we have added statement to clarify this in the revised manuscript.

(b) It is not clear to me why MARCM clones were induced and then flies grown at 18{degree sign}C? It would help to explain why they used this unconventional protocol.

We kept the flies at 18°C to avoid spontaneous clone.

(2) There are technical limitations with trying to conclude from double-knockdown experiments in the ISC lineage, such as those in Figure 1 where Dl and put are both being knocked down: depending on how fast both proteins are depleted, it may be that only one of them (put, for example) is inactivated and affects the fate decision prior to the other one (Dl) being depleted. Therefore, it is difficult to definitively conclude that the decision is independent of Dl ligand.

In our hand, Dl-RNAi is very effective and exhibited loss of N pathway activity (as determined by the N pathway reporter Su(H)-lacZ ) after RNAi for 8 days (Fig. 1D). Therefore, the ectopic Su(H)-lacZ expression in Punt Dl double RNAi (fig. 1E) is unlikely due to residual Dl expression. Nevertheless, we have changed the statement “BMP signaling blocks ligand-independent N activity” to” Loss of BMP signaling results in ectopic N pathway activity even when Dl is depleted”

(3) Additional quantification of many phenotypes would be desired.

(a) It would be useful to see esg-GFP cells/total cells and not just field as the density might change (2E for example).

We focused on R4 region for quantification where the cell density did not exhibit apparent change in different experimental groups. In addition, we have examined many guts for quantification. It is very unlikely that the difference in the esg-GFP+ cell number is caused by change in cell density.

(b) Similarly, for 2F and 2G, it would be nice to see the % of ISC/ total cell and EB/total cell and not only per esgGFP+ cell.

Unfortunately, we didn’t have the suggested quantification. However, we believe that quantification of the percentage of ISC or EB among all progenitor cells, as we did here, provides a meaningful measurement of the self-renewal status of each experimental group.

(c) Fig1: There is no quantification - specifically it would be interesting to know how many esg+ are su(H)lacZ positive in Put- Dl- condition compared to WT or Put- alone. What is the n?

Quantification of Fig.1 has been added. 

(d) Fig2: Pros + cells are not seen in the image? Are they all DllacZ+?

Anti-Pros and anti-E(spl)mβ-CD2 were stained in the same channel (magenta).  Pros+ exhibited “dot-like” nuclear staining while CD2 staining outlined the cell membrane of EBs. We have clarified this in the revised figure legend.

(e) Fig3: it would be nice to have the size clone quantification instead of the distribution between groups of 2 cell 3 cells 4 cell clones.

Because of the heterogeneity of clone size for each genotype, we chose to group clones based on their sizes ( 2, 3-6, 6-8, >8 cells) and quantified the distribution of individual groups for each genotype, which clearly showed an overall reduction in clone size for mad numb double mutant clones. We and others have used the same clone size analysis in previous studies (e.g., Tian and Jiang, eLife 2014).

(f) How many times were experiments performed?

All experiments were performed at least 3 times.

(4) The authors do not comment on the reduction of clone size in DSS treatment in Figure 6K. How do they interpret this? Does it conflict with their model of Bleo vs DSS?

Guts containing numb⁴ clones treated with DSS exhibited a slight reduction of clone size, evident by a higher percentage of 2-cell clones and lower percentage of > 8 cell clones. This reduction is less significant in guts containing numb¹⁵ clones. However, the percentage of Dl⁺-containing clones is similar between DSS and mock-treated guts. It is possible that ISC proliferation is lightly reduced due to numb⁴ mutation or the genetic background of this stock.

(5) There is probably a mistake on sentence line 314 -316 "Indeed, previous studies indicate that endogenous Numb was not undetectable by Numb antibodies that could detect Numb expression in the nervous system".

We have modified the sentence.

Reviewer #3 (Public review):

Summary:

The authors provide an in-depth analysis of the function of Numb in adult Drosophila midgut. Based on RNAi combinations and double mutant clonal analyses, they propose that Numb has a function in inhibiting Notch pathway to maintain intestinal stem cells, and is a backup mechanism with BMP pathway in maintaining midgut stem cell mediated homeostasis.

Strengths:

Overall, this is a carefully constructed series of experiments, and the results and statistical analyses provides believable evidence that Numb has a role, albeit weak compared to other pathways, in sustaining ISC and in promoting regeneration especially after damage by bleomycin, which may damage enterocytes and therefore disrupt BMP pathway more. The results overall support their claim.

The data are highly coherent, and support a genetic function of Numb, in collaborating with BMP signaling, to maintain the number and proliferative function of ISCs in adult midguts. The authors used appropriate and sophisticated genetic tools of double RNAi, mutant clonal analysis and dual marker stem cell tracing approaches to ensure the results are reproducible and consistent. The statistical analyses provide confidence that the phenotypic changes are reliable albeit weaker than many other mutants previously studied.

Weaknesses:

In the absence of Numb itself, the midgut has a weak reduction of ISC number (Fig. 3 and 5), as well as weak albeit not statistically significant reduction of ISC clone size/proliferation. I think the authors published similar experiments with BMP pathway mutants. The mad^1-2 allele used here as stated below may not be very representative of other BMP pathway mutants. Therefore, it could be beneficial to compare the number of ISC number and clone sizes between other BMP experiments to provide the readers with a clearer picture of how these two pathways individually contribute (stronger/weaker effects) to the ISC number and gut homeostasis.

Thanks for the comment. We have tested other components of BMP pathway in our previously study (Tian et al., 2014). More complete loss of BMP signaling (for example, Put clones, Put RNAi, Tkv/Sax double mutant clones or double RNAi) resulted in ISC loss regardless the status of numb, suggesting a more predominant role of BMP signaling in ISC self-renewal compared with Numb. We speculate that the weak stem cell loss phenotype associated with numb mutant clones in otherwise wild type background could be due to fluctuation of BMP signaling in homeostatic guts.

The main weakness of this manuscript is the analysis of the BMP pathway components, especially the mad^1-2 allele. The mad RNAi and mad^1-2 alleles (P insertion) are supposed to be weak alleles and that might be suitable for genetic enhancement assays here together with numb RNAi. However, the mad^1-2 allele, and sometimes the mad RNAi, showed weakly increased ISC clone size. This is kind of counter-intuitive that they should have a similar ISC loss and ISC clone size reduction.

We used mad^1-2 and mad RNAi here to test the genetic interaction with numb because our previous studies showed that partial loss of BMP signaling under these conditions did not cause stem cell loss, therefore, may provide a sensitized background to determine the role of Numb in ISC self-renewal. The increased proliferation of ISC/ clone size associated with mad^1-2 and mad RNAi is due to the fact that reduction of BMP signaling in either EC or EB non-autonomously induces stem cell proliferation. However, in mad numb double mutant clones, there was a reduction in clone size due to loss of ISC in many clones.

A much stronger phenotype was observed when numb mutants were subject to treatment of tissue damaging agents Bleomycin, which causes damage in different ways than DSS. Bleomycin as previously shown to be causing mainly enterocyte damage, and therefore disrupt BMP signaling from ECs more likely. Therefore, this treatment together with loss of numb led to a highly significant reduction of ISC in clones and reduction of clone size/proliferation. One improvement is that it is not clear whether the authors discussed the nature of the two numb mutant alleles used in this study and the comparison to the strength of the RNAi allele. Because the phenotypes are weak and more variable, the use of specific reagents is important.

We have included information about the two numb alleles in the “Materials and Methods”. numb¹⁵ is a null allele, and the nature of numb⁴ has not been elucidated. According to Domingos, P.M. et al., numb¹⁵ induced a more severe phenotype than numb⁴ did. Consistently, we also found that more numb¹⁵ mutant clones were void of stem cell than numb⁴ mutant clones.

Furthermore, the use of possible activating alleles of either or both pathways to test genetic enhancement or synergistic activation will provide strong support for the claims.

Activation of BMP (esgts>Tkv^CA) alone induced stem cell tumor (Tian et al., 2014) whereas overexpression of Numb did not induce increase stem cell number although overexpression of Numb in wing discs produced phenotypes indictive of inhibition of N (our unpublished observation), making it difficult to test the synergistic effect of activating both BMP and Numb.

Reviewer #1 (Recommendations for the authors):

- Cartoon of RGT in Fig 4 needs to be improved. We need to know what chromosome harbors the esgts. It is not sufficient to simply put the location of the ubi-GFP and ubi-RFP (on 19A) and not show the location of other components of the RGT system.

Thank you for the suggestion. We have revised the cartoon in Fig. 4 to include all three pairs of chromosomes and indicate where the esgts driver and UAS-RNAi are located. In addition, we have included the genotypes for all the genetic experiments in the Method section.

- Quantification of the results in Fig. 1

Quantification of Fig.1 has been added. 

- The authors need to explain the premise more carefully (see above) and explain whether or not they tested put, numb double knockdowns.

We have explained why not testing put numb double RNAi (see above).

Reviewer #2 (Recommendations for the authors):

The number of times the experiments have been performed would be useful to include.

This information has been added in the figure legends.

Author response:

We thank the reviewers for their thoughtful comments on our submitted manuscript.

The major point from all three reviewers was that the sensory inputs may be more complex than simply ASH and AWC, since mutations in osm-9 and tax-4 will affect many more sensory neurons. We fully agree. The differential effects of osm-9 and ta_x-_4 allowed us to recognize that there were two distinct afferent pathways operating simultaneously, mediating repulsion and attraction separately. However, it remains to be determined which sensory neurons are contributing to each pathway. We have planned a full analysis of the sensory inputs, not limited to just ASH and AWC, using neuron-specific rescue and neuron-specific chemogenetic inactivation (using HisCl1). While this analysis falls outside the scope of the present study, we will perform the inactivations of ASH and AWC and include the data for the revised version of this study. We expect to demonstrate whether ASH and AWC inputs are sufficient or whether other sensory neurons make significant contributions. Additionally, we will include chemotaxis dose-response data for osm-9 mutants as part of this analysis and make the minor corrections in data presentation requested.

Author response:

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

As to the exceptionally minor issue, namely, correction for multiple statistical tests (minor because the data and the error are presented in the text). We have now conducted one-way ANOVA to back the data displayed in Fig 4A., and Supp. Figs 19 and 21. In each case ANOVA revealed a highly significant difference among means: Dunnett’s post hoc test was then used to test each result against SBW25, with the multiple comparisons corrected for in the analysis.

This resulted in changes to the description of the statistical analysis in the following captions:

To Figure 4.

Where we previously referred to paired t-tests we now state:  ANOVA revealed a highly significant difference among means [F_7,16 = 8.19, p < 0.001] with Dunnett’s post-hoc test adjusted for multiple comparisons showing that five genotypes (*) differ significantly (p < 0.05) from SBW25.

To Supplementary Figure 19.

Where we previously referred to paired t-tests we now state: ANOVA revealed a highly significant difference among means [F_7,16 = 16.74, p < 0.001] with Dunnett’s post-hoc test adjusted for multiple comparisons showing that three genotypes (*) differ significantly (p < 0.05) from SBW25.

To Supplementary Figure 21.

Where we previously referred to paired t-tests we now state:  ANOVA revealed a highly significant difference among means [F_7,89 = 9.97, p < 0.0001] with Dunnett’s post-hoc test adjusted for multiple comparisons showing that SBW25 ∆mreB and SBW25 ∆PFLU4921-4925 are significantly different (*) from SBW25 (p < 0.05).

---

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors performed experimental evolution of MreB mutants that have a slow-growing round phenotype and studied the subsequent evolutionary trajectory using analysis tools from molecular biology. It was remarkable and interesting that they found that the original phenotype was not restored (most common in these studies) but that the round phenotype was maintained. 

Strengths: 

The finding that the round phenotype was maintained during evolution rather than that the original phenotype, rod-shaped cells, was recovered is interesting. The paper extensively investigates what happens during adaptation with various different techniques. Also, the extensive discussion of the findings at the end of the paper is well thought through and insighXul. 

Weaknesses: 

I find there are three general weaknesses: 

(1) Although the paper states in the abstract that it emphasizes "new knowledge to be gained" it remains unclear what this concretely is. On page 4 they state 3 three research questions, these could be more extensively discussed in the abstract. Also, these questions read more like genetics questions while the paper is a lot about cell biological findings. 

Thank you for drawing attention to the unnecessary and gratuitous nature of the last sentence of the Abstract. We are in agreement. It has been modified, and we have taken  advantage of additional word space to draw attention to the importance of the two competing (testable) hypotheses laid out in the Discussion. 

As to new knowledge, please see the Results and particularly the Discussion. But beyond this, and as recognised by others, there is real value for cell biology in seeing how (and whether) selection can compensate for effects that are deleterious to fitness. The results will very o_en depart from those delivered from, for example, suppressor analyses, or bottom up engineering. 

In the work recounted in our paper, we chose to focus – by way of proof-of principle – on the most commonly observed mutations, namely, those within pbp1A.  But beyond this gene, we detected mutations  in other components of the cell shape / division machinery whose connections are not yet understood and which are the focus of on-going investigation.  

As to the three questions posed at the end of the Introduction, the first concerns whether selection can compensate for deleterious effects of deleting mreB (a question that pertains to evolutionary aspects); the second seeks understanding of genetic factors; the third aims to shed light on the genotype-to-phenotype map (which is where the cell biology comes into play).  Given space restrictions, we cannot see how we could usefully expand, let alone discuss, the three questions raised at the end of the Introduction in restrictive space available in the Abstract.   

(2) It is not clear to me from the text what we already know about the restoration of MreB loss from suppressors studies (in the literature). Are there suppressor screens in the literature and which part of the findings is consistent with suppressor screens and which parts are new knowledge?  

As stated in the Introduction, a previous study with B. subtilis (which harbours three MreB isoforms and where the isoform named “MreB” is essential for growth under normal conditions), suppressors of MreB lethality were found to occur in ponA, a class A penicillin binding protein (Kawai et al., 2009). This led to recognition that MreB plays a role in recruiting Pbp1A to the lateral cell wall. On the other hand, Patel et al. (2020) have shown that deletion of classA PBPs leads to an up-regulation of rod complex activity. Although there is a connection between rod complex and class A PBPs, a further study has shown that the two systems work semi-autonomously (Cho et al., 2016). 

Our work confirms a connection between MreB and Pbp1A, and has shed new light on how this interaction is established by means of natural selection, which targets the integrity of cell wall. Indeed, the Rod complex and class A PBPs have complementary activities in the building of the cell wall with each of the two systems able to compensate for the other in order to maintain cell wall integrity. Please see the major part of the Discussion. In terms of specifics, the connection between mreB and pbp1A (shown by Kawai et al (2009)) is indirect because it is based on extragenic transposon insertions. In our study, the genetic connection is mechanistically demonstrated.  In addition, we capture that the evolutionary dynamics is rapid and we finally enriched understanding of the genotype-to-phenotype map.

(3) The clarity of the figures, captions, and data quantification need to be improved.  

Modifications have been implemented. Please see responses to specific queries listed below.

Reviewer #2 (Public Review): 

Yulo et al. show that deletion of MreB causes reduced fitness in P. fluorescens SBW25 and that this reduction in fitness may be primarily caused by alterations in cell volume. To understand the effect of cell volume on proliferation, they performed an evolution experiment through which they predominantly obtained mutations in pbp1A that decreased cell volume and increased viability. Furthermore, they provide evidence to propose that the pbp1A mutants may have decreased PG cross-linking which might have helped in restoring the fitness by rectifying the disorganised PG synthesis caused by the absence of MreB. Overall this is an interesting study. 

Queries: 

Do the small cells of mreB null background indeed have have no DNA? It is not apparent from the DAPI images presented in Supplementary Figure 17. A more detailed analysis will help to support this claim. 

It is entirely possible that small cells have no DNA, because if cell division is aberrant then division can occur prior to DNA segregation resulting in cells with no DNA. It is clear from microscopic observation that both small and large cells do not divide. It is, however, true, that we are unable to state – given our measures of DNA content – that small cells have no DNA. We have made this clear on page 13, paragraph 2.

What happens to viability and cell morphology when pbp1A is removed in the mreB null background? If it is actually a decrease in pbp1A activity that leads to the rescue, then pbp1A- mreB- cells should have better viability, reduced cell volume and organised PG synthesis. Especially as the PG cross-linking is almost at the same level as the T362 or D484 mutant.  

Please see fitness data in Supp. Fig. 13. Fitness of ∆mreB ∆pbp1A is no different to that caused by a point mutation. Cells remain round.  

What is the status of PG cross-linking in ΔmreB Δpflu4921-4925 (Line 7)? 

This was not analysed as the focus of this experiment was PBPs. A priori, there is no obvious reason to suspect that ∆4921-25 (which lacks oprD) would be affected in PBP activity.

What is the morphology of the cells in Line 2 and Line 5? It may be interesting to see if PG cross-linking and cell wall synthesis is also altered in the cells from these lines. 

The focus of investigation was restricted to L1, L4 and L7. Indeed, it would be interesting to look at the mutants harbouring mutations in :sZ, but this is beyond scope of the present investigation (but is on-going). The morphology of L2 and L5 are shown in Supp. Fig. 9.

The data presented in 4B should be quantified with appropriate input controls. 

Band intensity has now been quantified (see new Supp. Fig .20). The controls are SBW25, SBW25∆pbp1A, SBW25 ∆mreB and SBW25 ∆mreBpbp1A as explained in the paper.

What are the statistical analyses used in 4A and what is the significance value? 

Our oversight. These were reported in Supp. Fig. 19, but should also have been presented in Fig. 4A. Data are means of three biological replicates. The statistical tests are comparisons between each mutant and SBW25, and assessed by paired t-tests.  

A more rigorous statistical analysis indicating the number of replicates should be done throughout. 

We have checked and made additions where necessary and where previously lacking. In particular, details are provided in Fig. 1E, Fig. 4A and Fig. 4B. For Fig. 4C we have produced quantitative measures of heterogeneity in new cell wall insertion. These are reported in Supp. Fig. 21 (and referred to in the text and figure caption) and show that patterns of cell wall insertion in ∆mreB are highly heterogeneous.

Reviewer #3 (Public Review): 

This paper addresses an understudied problem in microbiology: the evolution of bacterial cell shape. Bacterial cells can take a range of forms, among the most common being rods and spheres. The consensus view is that rods are the ancestral form and spheres the derived form. The molecular machinery governing these different shapes is fairly well understood but the evolutionary drivers responsible for the transition between rods and spheres are not. Enter Yulo et al.'s work. The authors start by noting that deletion of a highly conserved gene called MreB in the Gram-negative bacterium Pseudomonas fluorescens reduces fitness but does not kill the cell (as happens in other species like E. coli and B. subtilis) and causes cells to become spherical rather than their normal rod shape. They then ask whether evolution for 1000 generations restores the rod shape of these cells when propagated in a rich, benign medium. 

The answer is no. The evolved lineages recovered fitness by the end of the experiment, growing just as well as the unevolved rod-shaped ancestor, but remained spherical. The authors provide an impressively detailed investigation of the genetic and molecular changes that evolved. Their leading results are: 

(1) The loss of fitness associated with MreB deletion causes high variation in cell volume among sibling cells a_er cell division. 

(2) Fitness recovery is largely driven by a single, loss-of-function point mutation that evolves within the first ~250 generations that reduces the variability in cell volume among siblings. 

(3) The main route to restoring fitness and reducing variability involves loss of function mutations causing a reduction of TPase and peptidoglycan cross-linking, leading to a disorganized cell wall architecture characteristic of spherical cells. 

The inferences made in this paper are on the whole well supported by the data. The authors provide a uniquely comprehensive account of how a key genetic change leads to gains in fitness and the spectrum of phenotypes that are impacted and provide insight into the molecular mechanisms underlying models of cell shape. 

Suggested improvements and clarifications include: 

(1) A schematic of the molecular interactions governing cell wall formation could be useful in the introduction to help orient readers less familiar with the current state of knowledge and key molecular players. 

We understand that this would be desirable, but there are numerous recent reviews with detailed schematics that we think the interested reader would be better consulting. These are referenced in the text.

(2) More detail on the bioinformatics approaches to assembling genomes and identifying the key compensatory mutations are needed, particularly in the methods section. This whole subject remains something of an art, with many different tools used. Specifying these tools, and the parameter sesngs used, will improve transparency and reproducibility, should it be needed. 

We overlooked providing this detail, which has now been corrected by provision of more information in the Materials and Methods. In short we used Breseq, the clonal option, with default parameters. Additional analyses were conducted using Genieous. The BreSeq output files are provided https://doi.org/10.17617/3.CU5SX1 (which include all read data).

(3) Corrections for multiple comparisons should be used and reported whenever more than one construct or strain is compared to the common ancestor, as in Supplementary Figure 19A (relative PG density of different constructs versus the SBW25 ancestor). 

The data presented in Supp Fig 19A (and Fig 4A) do not involve multiple comparisons. In each instance the comparison is between SBW25 and each of the different mutants. A paired t-test is thus appropriate.

(4) The authors refrain from making strong claims about the nature of selection on cell shape, perhaps because their main interest is the molecular mechanisms responsible. However, I think more can be said on the evolutionary side, along two lines. First, they have good evidence that cell volume is a trait under strong stabilizing selection, with cells of intermediate volume having the highest fitness. This is notable because there are rather few examples of stabilizing selection where the underlying mechanisms responsible are so well characterized. Second, this paper succeeds in providing an explanation for how spherical cells can readily evolve from a rod-shaped ancestor but leaves open how rods evolved in the first place. Can the authors speculate as to how the complex, coordinated system leading to rods first evolved? Or why not all cells have lost rod shape and become spherical, if it is so easy to achieve? These are important evolutionary questions that remain unaddressed. The manuscript could be improved by at least flagging these as unanswered questions deserving of further attention. 

These are interesting points, but our capacity to comment is entirely speculative. Nonetheless, we have added an additional paragraph to the Discussion that expresses an opinion that has yet to receive attention:

“Given the complexity of the cell wall synthesis machinery that defines rod-shape in bacteria, it is hard to imagine how rods could have evolved prior to cocci. However, the cylindrical shape offers a number of advantages. For a given biomass (or cell volume), shape determines surface area of the cell envelope, which is the smallest surface area associated with the spherical shape. As shape sets the surface/volume ratio, it also determines the ratio between supply (proportional to the surface) and demand (proportional to cell volume). From this point of view, it is more efficient to be cylindrical (Young 2006). This also holds for surface attachment and biofilm formation (Young 2006). But above all, for growing cells, the ratio between supply and demand is constant in rod shaped bacteria, whereas it decreases for cocci. This requires that spherical cells evolve complex regulatory networks capable of maintaining the correct concentration of cellular proteins despite changes in surface/volume ratio. From this point of view, rod-shaped bacteria offer opportunities to develop unsophisticated regulatory networks.”

why not all cells have lost rod shape and become spherical.

Please see Kevin Young’s 2006 review on the adaptive significance of cell shape

The value of this paper stems both from the insight it provides on the underlying molecular model for cell shape and from what it reveals about some key features of the evolutionary process. The paper, as it currently stands, provides more on which to chew for the molecular side than the evolutionary side. It provides valuable insights into the molecular architecture of how cells grow and what governs their shape. The evolutionary phenomena emphasized by the authors - the importance of loss-of-function mutations in driving rapid compensatory fitness gains and that multiple genetic and molecular routes to high fitness are o_en available, even in the relatively short time frame of a few hundred generations - are wellunderstood phenomena and so arguably of less broad interest. The more compelling evolutionary questions concern the nature and cause of stabilizing selection (in this case cell volume) and the evolution of complexity. The paper misses an opportunity to highlight the former and, while claiming to shed light on the latter, provides rather little useful insight. 

Thank you for these thoughts and comments. However, we disagree that the experimental results are an overlooked opportunity to discuss stabilising selection. Stabilising selection occurs when selection favours a particular phenotype causing a reduction in underpinning population-level genetic diversity. This is not happening when selection acts on SBW25 ∆mreB leading to a restoration of fitness. Driving the response are biophysical factors, primarily the critical need to balance elongation rate with rate of septation. This occurs without any change in underlying genetic diversity.  

Recommendations for the authors:  

Reviewer 1 (Recommendations for the Authors): 

Hereby my suggestion for improvement of the quantification of the data, the figures, and the text. 

-  p 14, what is the unit of elongation rate?  

At first mention we have made clear that the unit is given in minutes^-1

-  p 14, please give an error bar for both p=0.85 and f=0.77, to be able to conclude they are different 

Error on the probability p is estimated at the 95% confidence interval by the formula:1.96 , where N is the total number of cells. This has been added in the paragraph p »probability » of the Image Analysis section in the Material and Methods. 

We also added errors on p measurement in the main text.

-  p 14, all the % differences need an errorbar 

The error bars and means are given in Fig 3C and 3D.

-  Figure 1B adds units to compactness, and what does it represent? Is the cell size the estimated volume (that is mentioned in the caption)? Shouldn't the datapoints have error bars? 

Compactness is defined in the “Image Analysis” section of the Material and Methods. It is a dimensionless parameter. The distribution of individual cell shapes / sizes are depicted in Fig 1B. Error does arise from segmentation, but the degree of variance (few pixels) is much smaller than the representations of individual cells shown.

-  Figure 1C caption, are the 50.000 cells? 

Correct. Figure caption has been altered.

-  Figure 1D, first the elongation rate is described as a volume per minute, but now, looking at the units it is a rate, how is it normalized? 

Elongation rate is explained in the Materials and Methods (see the image analysis section) and is not volume per minute. It is dV/dt = r*V (the unit of r is min^-1). Page 9 includes specific mention of the unit of r.

-  Figure 1E, how many cells (n) per replicate? 

Our apologies. We have corrected the figure caption that now reads:

“Proportion of live cells in ancestral SBW25 (black bar) and ΔmreB (grey bar) based on LIVE/DEAD BacLight Bacterial Viability Kit protocol. Cells were pelleted at 2,000 x g for 2 minutes to preserve ΔmreB cell integrity. Error bars are means and standard deviation of three biological replicates (n>100).”

-  Figure 1G, how does this compare to the wildtype 

The volume for wild type SBW25 is 3.27µm^3 (within the “white zone”). This is mentioned in the text.

-  Figure 2B, is this really volume, not size? And can you add microscopy images? 

The x-axis is volume (see Materials and Methods, subsection image analysis). Images are available in Supp. Fig. 9.

-  Figure 3A what does L1, L4 and L7 refer too? Is it correct that these same lines are picked for WT and delta_mreB 

Thank you for pointing this out. This was an earlier nomenclature. It was shorthand for the mutants that are specified everywhere else by genotype and has now been corrected. 

-  Figure 3c: either way write out p, so which probability, or you need a simple cartoon that is plotted. 

The value p is the probability to proceed to the next generation and is explained in Materials and Methods  subsection image analysis.  We feel this is intuitive and does not require a cartoon. We nonetheless added a sentence to the Materials and Methods to aid clarity.

-  Figure 4B can you add a ladder to the gel? 

No ladder was included, but the controls provide all the necessary information. The band corresponding to PBP1A is defined by presence in SBW25, but absence in SBW25 ∆pbp1A.

-  Figure 4c, can you improve the quantification of these images? How were these selected and how well do they represent the community? 

We apologise for the lack of quantitative description for data presented in Fig 4C. This has now been corrected. In brief, we measured the intensity of fluorescent signal from between 10 and 14 cells and computed the mean and standard deviation of pixel intensity for each cell. To rule out possible artifacts associated with variation of the mean intensity, we calculated the ratio of the standard deviation divided by the square root of the mean. These data reveal heterogeneity in cell wall synthesis and provide strong statistical support for the claim that cell wall synthesis in ∆mreB is significantly more heterogeneous than the control. The data are provided in new Supp. Fig. 21. 

Minor comments: 

-  It would be interesting if the findings of this experimental evolution study could be related to comparative studies (if these have ever been executed).  

Little is possible, but Hendrickson and Yulo published a portion of the originally posted preprint separately. We include a citation to that paper. 

-  p 13, halfway through the page, the second paragraph lacks a conclusion, why do we care about DNA content? 

It is a minor observation that was included by way of providing a complete description of cell phenotype.  

-  p 17, "suggesting that ... loss-of-function", I do no not understand what this is based upon. 

We show that the fitness of a pbp1A deletion is indistinguishable from the fitness of one of the pbp1A point mutants. This fact establishes that the point mutation had the same effects as a gene deletion thus supporting the claim that the point mutations identified during the course of the selection experiment decrease (or destroy) PBP1A function.

-  p 25, at the top of the page: do you have a reference for the statement that a disorganized cell wall architecture is suited to the topology of spherical cells? 

The statement is a conclusion that comes from our reasoning. It stems from the fact that it is impossible to entirely map the surface of a sphere with parallel strands.

Author response:

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

We are disappointed that the reviewers do not acknowledge that our data constitute a major step forward for the field. We will prepare a revised version that takes care of the remaining small issues concerning the technical descriptions and a detailed response to the current round of comments. We will also add a summary of the major new findings of our study.

---

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

We appreciate the time of the reviewers and their detailed comments, which have helped to improve the manuscript.

Our study presents the largest systematic dataset so far on the evolution of sex-biased gene expression in animals. It is also the first that explores the patterns of individual variation in sex-biased gene expression and the SBI is an entirely new procedure to directly visulize these variance patterns in an intuitive way.

Also, we should like to point out that our study contradicts recent conclusions that had suggested that a substantial set of sex-biased genes has conserved functions between humans and mice and that mice can therefore be informative for gender-specific medicine studies. Our data suggest that only a very small set of genes are conserved in their sex-biased expression between mice and humans in more than one organ.

In the revised version we have made the following major updates:

- added a rate comparison of gene regulation turnover between sex-biased and non-sex-biased genes

- added additional statistics to the variance comparisons and selection tests

- added a regulatory module analysis that shows that much of the gene turnover happens within modules

- added a mosaic pattern analysis that shows the individual complexity of sex-biased patterns

- extended introduction and discussion

Reviewer #1 (Public Review):<br /> The authors describe a comprehensive analysis of sex-biased expression across multiple tissues and species of mouse. Their results are broadly consistent with previous work, and their methods are robust, as the large volume of work in this area has converged toward a standardized approach.

I have a few quibbles with the findings, and the main novelty here is the rapid evolution of sex-biased expression over shorter evolutionary intervals than previously documented, although this is not statistically supported. The other main findings, detailed below, are somewhat overstated.

(1) In the introduction, the authors conflate gametic sex, which is indeed largely binary (with small sperm, large eggs, no intermediate gametic form, and no overlap in size) with somatic sexual dimorphism, which can be bimodal (though sometimes is even more complicated), with a large variance in either sex and generally with a great deal of overlap between males and females. A good appraisal of this distinction is at . This distinction in gene expression has been recognized for at least 20 years, with observations that sex-biased expression in the soma is far less than in the gonad.

For example, the authors frame their work with the following statement:

"The different organs show a large individual variation in sex-biased gene expression, making it impossible to classify individuals in simple binary terms. Hence, the seemingly strong conservation of binary sex-states does not find an equivalent underpinning when one looks at the gene-expression makeup of the sexes"

The authors use this conflation to set up a straw man argument, perhaps in part due to recent political discussions on this topic. They seem to be implying one of two things. a) That previous studies of sex-biased expression of the soma claim a binary classification. I know of no such claim, and many have clearly shown quite the opposite, particularly studies of intra-sexual variation, which are common - see https://doi.org/10.1093/molbev/msx293, https://doi.org/10.1371/journal.pgen.1003697, https://doi.org/10.1111/mec.14408, https://doi.org/10.1111/mec.13919, https://doi.org/10.1111/j.1558-5646.2010.01106.x for just a few examples. Or b) They are the first to observe this non-binary pattern for the soma, but again, many have observed this. For example, many have noted that reproductive or gonad transcriptome data cluster first by sex, but somatic tissue clusters first by species or tissue, then by sex (https://doi.org/10.1073/pnas.1501339112, https://doi.org/10.7554/eLife.67485)

Figure 4 illustrates the conceptual difference between bimodal and binary sexual conceptions. This figure makes it clear that males and females have different means, but in all cases the distributions are bimodal.

I would suggest that the authors heavily revise the paper with this more nuanced understanding of the literature and sex differences in their paper, and place their findings in the context of previous work.

We are sorry that our introduction seems to have been too short to make our points sufficiently clear. Of course, overlapping somatic variation has been shown for morphological characters, but we were aiming to assess this at the sex-biased transcriptome level. Previous studies looking at sex-biased genes were usually limited by the techniques that were available at their times, resulting in a focus on gonads in most studies and almost all have too few individuals included to study within-group variation. We detail this below for the papers that are mentioned by the referee. In view of this, we cite them now as examples for the prevalent focus on gonadal comparisons in most studies. Only Scharmann et al. 2021 on plant leaf dimorphism is indeed relevant for our study with respect to its general findings and we make now extensive reference to it. In addition, we have generally modified the introduction and substantially extended the discussion to make our points clear.

Snell-Rood 2010: the paper focuses on sex-specific morphological structures in beetles. It samples six somatic tissues for four individuals each of each class. Analysis is done via microarray hybridizations. While categorial differences were traced, variability between individuals was not discussed. By today´s standards, microarrays have anyway too much technical variability to even consider such a discussion.

Pointer et al. 2013: this paper studies three sexual phenotypes in a bird species, females, dominant males and subordinate males. Tissues include telencephalon, spleen and left gonad. The focus of the analysis is on the gonads, since only few sex-biased genes were found in spleen and brain (according to suppl. Table S1, 0 for the spleen and 2 for the brain). No inferences could be made on somatic variation.

Harrison 2015: this paper focuses on gonads plus spleen in six bird species with between 2-6 individuals for each sex collected. In the spleen, only one female biased gene and no male biased gene was detected. Hence, the data do not allow to infer patterns of somatic variation.

Dean et al. 2016: this paper compares four categories of fish caught around nests, with four to seven individuals per category. Only gonads were analyzed, hence no inferences could be made about somatic variability between individuals.

Cardoso et al. 2017: this paper test categories of fish with alternative reproductive tactics based on brain transcriptomes. While it uses 9-10 individuals per category, it uses pools for sequencing with two pools per category. This does not allow to make any inference on individual variation.

Todd et al 2017: this paper focuses on three categories of a fish species, females and dominant and sneaker males. It uses brain and gonads as samples with five individuals each for each category. For the brain, more different genes were found between the two types of males, rather than between females and males (3 and 9 respectively). The paper focuses on individual gene descriptions and does not mention somatic variation.

Scharmann 2021: the paper focuses on 10 species of plants with sexually dimorphic leafs. 5-6 individuals were sampled per sex. The major finding is that sex-biased gene expression does not correlate with the degree of sexual dimorphism of the leafes. The study shows also a fast evolution of sex-biased expression and states that signatures of adaptive evolution are weak. But it does not discuss variance patterns within populations.

(2) The authors also claim that "sexual conflict is one of the major drivers of evolutionary divergence already at the early species divergence level." However, making the connection between sex-biased genes and sexual conflict remains fraught. Although it is tempting to use sex-biased gene expression (or any form of phenotypic dimorphism) as an indicator of sexual conflict, resolved or not, as many have pointed out, one needs measures of sex-specific selection, ideally fitness, to make this case (https://doi.org/10.1086/595841, 10.1101/cshperspect.a017632). In many cases, sexual dimorphism can arise in one sex only without conflict (e.g. 10.1098/rspb.2010.2220). As such, sex-biased genes alone are not sufficient to discriminate between ongoing and resolved conflict.

We imply sexual conflict as a driver of genomic divergence patterns in a similar way as it has been done by many authors before (e.g. Mank 2017a, Price et al. 2023, Tosto et al. 2023). While we fully appreciate the point of the referee, we do not really see where we deviate from the standard wording that is used in the context of genomic data. In such data, it is of course usually assumed that they represent solved conflicts (Figure 1D in Cox and Calsbeek) where selection differentials would not be measurable anyway. (Please note also that the phylogenetic approach used in Oliver and Monteiro 2010 becomes rather problematic in view of introgressive hybridization patterns in butterflies), We have extended the discussion to address this.

(3) To make the case that sex-biased genes are under selection, the authors report alpha values in Figure 3B. Alpha value comparisons like this over large numbers of genes often have high variance. Are any of the values for male- female- and un-biased genes significantly different from one another? This is needed to make the claim of positive selection.

Sorry, we had accidentally not included the statistics in the final version of the figure. We have added this now in the supplementary table but have also generally changed the statistical approach and the design of the figure.

Reviewer #2 (Public Review):

The manuscript by Xie and colleagues presents transcriptomic experiments that measure gene expression in eight different tissues taken from adult female and male mice from four species. These data are used to make inferences regarding the evolution of sex-biased gene expression across these taxa. The experimental methods and data analysis are appropriate; however, most of the conclusions drawn in the manuscript have either been previously reported in the literature or are not fully supported by the data.

We are not aware of any study that has analyzed somatic sex-biased expression in such a large and taxonomically well resolved closely related taxa of animals. Only the study by Scharman et al. 2021 on plant leaves comes close to it, but even this did not specifically analyze the intragroup variation aspects. Of course, some of our results confirm previous conclusions, but we should still like to point out that they go far beyond them.

There are two ways the manuscript could be modified to better strengthen the conclusions.

First, some of the observed differences in gene expression have very little to no effect on other phenotypes, and are not relevant to medicine or fitness. Selectively neutral gene expression differences have been inferred in previous studies, and consistent with that work, sex-biased and between-species expression differences in this study may also be enriched for selectively neutral expression differences. This idea is supported by the analysis of expression variance, which indicates that genes that show sex-biased expression also tend to show more inter-individual variation. This perspective is also supported by the MK analysis of molecular evolution, which suggests that positive selection is more prevalent among genes that are sex-biased in both mus and dom, and genes that switch sex-biased expression are under less selection at the level of both protein-coding sequence and gene expression.

We have now revisited these points by additional statistical analysis of the variance patterns and an extended discussion under the heading "Neutral or adaptive?". 

As an aside, I was confused by (line 176): "implying that the enhanced positive selection pressure is triggered by their status of being sex-biased in either taxon." - don't the MK values suggest an excess of positive selection on genes that are sex-biased in both taxa?

There are different sets of genes that are sex-biased in these two taxa - hence this observation is actually a strong argument for selection on these genes. We have changed the correspondiung text to make this clearer.

Without an estimate of the proportion of differentially expressed genes that might be relevant for broader physiological or organismal phenotypes, it is difficult to assess the accuracy and relevance of the manuscript's conclusions. One (crude) approach would be to analyze subsets of genes stratified by the magnitude of expression differences; while there is a weak relationship between expression differences and fitness effects, on average large gene expression differences are more likely to affect additional phenotypes than small expression differences.

We agree that it remains a challenge to show functional effects for the sex-biased genes. The argument that they should have a function is laid out above (and stated in many reviews on the topic). To use the expression level as a proxy of function does not seem justified, given the current literature. For example, genes that are highly conected in modules are not necessrily highly expressed (e.g. transcription factors). Also, genes may be highly expressed in a rare cell type of an organ and have an important funtion there, but this would not show up across the RNA of the whole organ. The most direct functional relationship between sex-biased expression and phenotype comes from the human data in Naqvi et al. 2019 - which we had cited.

Another perspective would be to compare the within-species variance to the between-species variance to identify genes with an excess of the latter relative to the former (similar logic to an MK test of amino acid substitutions).

Such an analysis was actually our intial motivation for this study. However, the new (and surprising!) result is that the status of being sex-biased shows such a high turnover that not many genes are left per organ where one could even try to make such a test. However, we have extended the variance analysis with reciprocal gene sets (as we had done it for the MK test) and extended the discussion on the topic, including citation of our prior work on these questions.

Second, the analysis could be more informative if it distinguished between genes that are expressed across multiple tissues in both sexes that may show greater expression in one sex than the other, versus genes with specialized function expressed solely in (usually) reproductive tissues of one sex (e.g. ovary-specific genes). One approach to quantify this distinction would be metrics like those used defined by [Yanai I, et al. 2005. Genome-wide midrange transcription profiles reveal expression-level relationships in human tissue specification. Bioinformatics 21:650-659.] These approaches can be used to separate out groups of genes by the extent to which they are expressed in both sexes versus genes that are primarily expressed in sex-specific tissue such as testes or ovaries. This more fine-grained analysis would also potentially inform the section describing the evolution/conservation of sex-biased expression: I expect there must be genes with conserved expression specifically in ovaries or testes (these are ancient animal structures!) but these may have been excluded by the requirement that genes be sex-biased and expressed in at least two organs.

Given that our study focuses on somatic sex-biased genes, we refrain from a comparative analysis of genes that are only expressed in the sex-organs in this paper. With respect to sharing of sex-biased gene expresssion between the somatic tissues, we show in Figure 8 that there are only very few of them (8 female-biased and 3 male-biased). A separate statistical treatment is not possible for this small set of genes.

There are at least three examples of statements in the discussion that at the moment misinterpret the experimental results.

The discussion frames the results in the context of sexual selection and sexually antagonistic selection, but these concepts are not synonymous. Sexual selection can shape phenotypes that are specific to one sex, causing no antagonism; and fitness differences between males and females resulting from sexually antagonistic variation in somatic phenotypes may not be acted on by sexual selection. Furthermore, the conditions promoting and consequence of both kinds of selection can be different, so they should be treated separately for the purposes of this discussion.

We cannot make such a distinction for gene expression patterns - and we are not aware that this was done before in the literature (except gene expression was directly linked to a morphological structure). We have updated this discussion accordingly.

The discussion claims that "Our data show that sex-biased gene expression evolves extremely fast" but a comparison or expectation for the rate of evolution is not provided. Many other studies have used comparative transcriptomics to estimate rates of gene expression evolution between species, including mice; are the results here substantially and significantly different from those previous studies? Furthermore, the experimental design does not distinguish between those gene expression phenotypes that are fixed between species as compared to those that are polymorphic within one or more species which prevents straightforward interpretation of differences in gene expression as interspecific differences.

Our statement was in relation to the comparison between somatic and gondadal gene turnover, as well as the comparison to humans. We have now included an additional analysis for a direct comparison with non-sex-biased genes in the same populations (Figure 2B). Note that gene expression variances cannot get fixed anyway, they can only become different in average and magnitude.

The conclusion that "Our results show that most of the genetic underpinnings of sex differences show no long-term evolutionary stability, which is in strong contrast to the perceived evolutionary stability of two sexes" - seems beyond the scope of this study. This manuscript does not address the genetic underpinnings of sex differences (this would involve eQTL or the like), rather it looks at sex differences in gene expression phenotypes.

This comes back to the points discussed above about the validity to infer function from sex-biased expression. We have updated the text to clarify this.

Simply addressing the question of phenotypic evolutionary stability would be more informative if genes expressed specifically in reproductive tissues were separated from somatic sex-biased genes to determine if they show similar patterns of expression evolution.

Our study is generally focused on somatic gene expression. The comparison with reproductive tissues serves merely as a reference. Since they are of course very different tissues, they should not be compared with each other in the same way. We have now specifically addressed this point in the discussion.

Reviewer #3 (Public Review):

This manuscript reports some interesting and important patterns. The results on sex-bias in different tissues and across four taxa would benefit from alternative (or additional) presentation styles. In my view, the most important results are with respect to alpha (fraction of beneficial amino acid changes) in relation to sex-bias (though the authors have made this as a somewhat minor point in this version).

The part that the authors emphasize I don't find very interesting (i.e., the sexes have overlapping expression profiles in many nongonadal tissues), nor do I believe they have the appropriate data necessary to convincingly demonstrate this (which would require multiple measures from the same individual).

This is the first study that reports such overlaps and we show that this is not always the case (e.g. liver and kidney data in mice). We are not aware of any preditions of how such patterns would look like and how they would evolve - why should such a new finding not be interesting? Concerning the appropriateness of the data we do not agree with the point the referee makes - see response below.

This study reports several interesting patterns with respect to sex differences in gene expression across organs of four mice taxa. An alternative presentation of the data would yield a clearer and more convincing case that the patterns the authors claim are legitimate.

I recommend that the authors clarify what qualifies as "sex-bias".

This is defined by the statistical criteria that we have applied, following the general standard of papers on this topic.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) "However, already Darwin has pointed out that the phenotypes of the sexes should evolve fast". I think the authors mean that Darwin was quick to point out that sex-specific phenotypes evolve quickly".

We have modified this text part.

(2) Non-gonadal is more often referred to as somatic. I would encourage the authors to use this more common term for accessibility.

We have adopted this term

(3) Figure 5 is interesting, however, it is difficult to know whether the decreased bimodality in humans compared to mice is biological or technical due to the differences in the underlying data. For example, the mouse samples tightly controlled age and environmental conditions within each species. It is not possible to do that with human samples, and there are very good reasons to think that these factors will affect variance in both sexes.

Yes, this is certainly true and we know this also from other comparative data between mice and humans. Still, this is human reality vs mouse artificialness. We pick this now up in the discussion.

(4) Line 273. The large numbers of cells needed for single-cell analysis require that most studies pool multiple samples, however these pools are helpful in themselves. This approach was used by https://doi.org/10.1093/evlett/qrad013 to quantify the degree of sex-bias within cell types across multiple tissues and to compare how bulk and single-cell sex-bias measures compare. Sex-bias in some somatic cell types was very high, even when bulk sex-bias in those tissues was not. This suggests that the bulk data the authors use in this study may in fact obscure the pattern of sex-bias.

Yes, we agree, and this is exactly how we did the analysis and interpretation, based on the cited paper.

(5)- Line 379 "Total RNAs were" should be "Total RNA was"

Corrected

References cited in this review and which should be included in the manuscript :

Sam L Sharpe, Andrew P Anderson, Idelle Cooper, Timothy Y James, Alexandra E Kralick, Hans Lindahl, Sara E Lipshutz, J F McLaughlin, Banu Subramaniam, Alicia Roth Weigel, A Kelsey Lewis, Sex and Biology: Broader Impacts Beyond the Binary, Integrative, and Comparative Biology, Volume 63, Issue 4, October 2023, Pages 960-967.

Included

Masculinization of Gene Expression Is Associated with Exaggeration of Male Sexual Dimorphism Pointer MA, Harrison PW, Wright AE, Mank JE (2013) Masculinization of Gene Expression Is Associated with Exaggeration of Male Sexual Dimorphism. PLOS Genetics 9(8): e1003697.

Included

Erica V Todd, Hui Liu, Melissa S Lamm, Jodi T Thomas, Kim Rutherford, Kelly C Thompson, John R Godwin, Neil J Gemmell, Female Mimicry by Sneaker Males Has a Transcriptomic Signature in Both the Brain and the Gonad in a Sex-Changing Fish, Molecular Biology and Evolution, Volume 35, Issue 1, January 2018, Pages 225-241.

Included

Cardoso SD, Gonçalves D, Goesmann A, Canário AVM, Oliveira RF. Temporal variation in brain transcriptome is associated with the expression of female mimicry as a sequential male alternative reproductive tactic in fish. Mol Ecol. 2018; 27: 789-803.

Included

Dean, R., Wright, A.E., Marsh-Rollo, S.E., Nugent, B.M., Alonzo, S.H. and Mank, J.E. (2017), Sperm competition shapes gene expression and sequence evolution in the ocellated wrasse. Mol Ecol, 26: 505-518.

Included

Emilie C. Snell‐Rood, Amy Cash, Mira V. Han, Teiya Kijimoto, Justen Andrews, Armin P. Moczek, DEVELOPMENTAL DECOUPLING OF ALTERNATIVE PHENOTYPES: INSIGHTS FROM THE TRANSCRIPTOMES OF HORN‐POLYPHENIC BEETLES, Evolution, Volume 65, Issue 1, 1 January 2011.

Not included, since its technical approach is not really comparable

Harrison PW, Wright AE, Zimmer F, Dean R, Montgomery SH, Pointer MA, Mank JE (2015) Sexual selection drives evolution and rapid turnover of male gene expression. Proceedings of the National Academy of Sciences, USA 112: 4393-4398.

Included

Mathias Scharmann, Anthony G Rebelo, John R Pannell (2021) High rates of evolution preceded shifts to sex-biased gene expression in Leucadendron, the most sexually dimorphic angiosperms eLife 10:e67485.

Included

Sexually Antagonistic Selection, Sexual Dimorphism, and the Resolution of Intralocus Sexual Conflict. Robert M. Cox and Ryan Calsbeek , The American Naturalist 2009 173:2, 176-187.

Included

Ingleby FC, Flis I, Morrow EH. Sex-biased gene expression and sexual conflict throughout development. Cold Spring Harb Perspect Biol. 2014 Nov 6;7(1):a017632.

Included

Oliver JC, Monteiro A 2011. On the origins of sexual dimorphism in butterflies. Proc Biol Sci 278: 1981-1988.

Included

Iulia Darolti, Judith E Mank, Sex-biased gene expression at single-cell resolution: cause and consequence of sexual dimorphism, Evolution Letters, Volume 7, Issue 3, June 2023, Pages 148-156.

Included

Reviewer #2 (Recommendations For The Authors):

I am concerned the smoothed density plots in Figure 4 may be providing a misleading sense of the distributions since each distribution is inferred from only 9 values. A boxplot might better represent the data to the reader.

Boxplots with 9 values are much more difficult to interpret for a reader, this is the very reason why one tends to smoothen them. In this way, they also become similar to the standard plots that are used for showing morphological variation between the sexes. Note that the original data are availble for the individual values, if these are of special interest in some cases. In addition, our new “mosaic” analysis (Figure 6) provides another presentation for readers.

Line 235: "the overall numbers are lower" I assume this is the number of genes included in the analyses, but this should be explicitly stated.

Clarified in the text

The analysis of gene expression from different brain regions in control individuals from the Alzheimer's study (line 273) suffers from low power and it is not clear to me how much taking samples from different brain regions eliminates the issue of different cell types within a sample (the stated motivation for this analysis). While I support publishing negative results, this section does not feel like it adds much to the manuscript and could be cut in my opinion.

This is actually a study on single cell types, differentiating each of them. We are sorry that the text was apparently unclear about this. Given that there are studies that show the importance of looking at single cell data, we still think that is a suitable analysis. We have updated the text to make it clearer.

It might be useful to separate out X-linked genes from autosomal genes to see if they show consistent patterns with regard to sex-bias.

We have added this information in suppl. Table S2 and include some description in the text.

Reviewer #3 (Recommendations For The Authors):

Comments follow the order of the Results section:

(1) The latter half of this line in the Methods is too vague to be helpful: "We have explored a range of cutoffs and found that a sex-bias ratio of 1.25-fold difference of MEDIAN expression values combined with a Wilcoxon rank sum test and Benjamini-Hochberg FDR correction (using FDR <0.1 as cutoff) (Benjamini & Hochberg, 1995) yields the best compromise between sensitivity and specificity". What precisely is meant by "the best compromise between sensitivity and specificity"?

We explain now that this was based on pre-tests with comparing randomized with actual data. However, we agree that this is in the end a subjective decision, but there is no single standard used in the literature, especially when somatic organs are included. We consider our criteria as rather stringent.

(2) The 1.25 number for sex bias is, ultimately, an arbitrary cut-off. It is common in this literature to choose some arbitrary level and, in this sense, the authors are following common practice. The choice of 1.25 should be stated in the main text as it is a lower (but not reasonable) value than has been used in many other papers.

It is not only the cutoff, but also the Wilcoxon test and FDR correction that defines the threshold. See also comment above.

(3) In truth, dimorphism is continuous rather than discrete (i.e, greater or less than 1.25 fold different). Thus, where possible it would be useful to present results in a fashion that allows readers to see the continuous range of ratios rather than having to worry about whether the patterns are due to the rather arbitrary choices of how genes were binned into sex-bias categories.

It is necessary to work with cutoffs in such cases - and this is the usual practice for any such paper. But we provide now in Figure 1 Figure supplement 1 plots with the female/male ratio distributions.

a) Number of genes that are female- / male-biased. I would like to be able to see a version of Figure 1 showing the full distribution of TPM ratios rather than bar graphs of the numbers of (arbitrarily defined) female- and male-biased genes. This will be, of course, a larger figure (a full distribution rather than 2 bars for each species for each organ) and so could be relegated to Supplementary Material (assuming the message of that figure is the same as the current Figure 1).

This is a very unusual request, given that no other paper has done this either. It would indeed result in a non-managable figure size, or many separate figures that would be difficult to scrutinize. Note that there would be one plot of two (female and male) TPM distributions for each sex-biased gene in each organ and each taxon, leading to hundreds of thousands of plots. We think that by providing the general distributions as plots (see above), and the original data as supplements is sufficient.

b) Turnover of genes with sex bias. This important issue is addressed in Figure 2. First, it is not precisely clear what "percentages of sums of shared genes for any pairwise comparison" in Figure 2 legend means and no further detail is given in the Methods; this must be made clearer or the info in Figure 2 is meaningless. Regardless, this approach again relies heavily on the arbitrary criterion of defining sex-bias. Thus, I would like to see correlation plots of the log(TPM ratio) between taxa as done in the classic multispecies fly paper of Zhang et al. 2007. In Figure 2 it is quite clear that male-biased genes evolve with respect to sex bias more rapidly than female-biased genes.

We have provided a better explanation of this analysis. Note that the Zhang et al. 2007 paper was not focussing on somatic expression and covers a much broader evolutionary spectrum. Hence, the results are not comparable. Also, we doubt that it would be so helpful to generate a huge figure with all these plots.

(4) Is there a simpler explanation for the results in the "Variance patterns" section? The total variance for any variable can be decomposed into the variance within and among "groups". If we use "sex" as the group, then there are genes - labelled sex-biased genes - that were identified as such, in essence, because they have high among-group variance. Given that we then know a priori at the start of this section of sex-biased genes have high among-group variance, is it at all surprising that they have higher total variance than the unbiased genes (which we know a priori have low among-group variance)? Perhaps I misunderstood the point of this section. Maybe it would be more meaningful to examine the WITHIN-SEX variance (averaged across the two sexes) instead.

We did calculate IQR/median (“normalized variance”) with the nine mice for each gene and each sex in each organ, hence sex is not a variance factor in this calculation. The algorithm steps are outlined in suppl. Table S17. We have now also added a variance calculation for reciprocal gene sets and added an extended discussion of these results.

(5) Analysis of alpha for sex-biased genes. This was the most interesting part of this manuscript to me.

(a) More information about what SNVs were used is required.

i. Were only sites where SPR was fixed used? (If not, how was polarization done?)

ii. Were sites only considered diverged if they were fixed for different bases in DOM and MUS? (If not, what was the criteria?)

iii. Using, say, DOM as the focal species, a site must be polymorphic in DOM. But did its status (polymorphic/fixed) in MUS matter?

We have added a more detailed description on this in the Methods section. For the direct answers of the three questions: (i) yes; (ii) yes; (iii) no, considering that DOM and MUS are two subspecies of Mus musculus separating recently, a variant might occur before separating and there might be gene flow between them.

(b) A particularly interesting part of the analysis is the investigation of alpha for genes that are NOT sex-biased in one taxa but are sex-biased in the other. At the moment (as I understand it), alpha is only calculated for these genes in the taxa where they are NOT sex-biased (and this alpha value can be compared to the alpha of sex-biased genes and of unbiased genes in that taxa). I would like to see both sets of genes (set 1: those sex-biased in MUS and not in DOM; set 2: those sex-biased DOM and not in MUS) analyzed in each of the 2 species, with results presented in a 2x2 table.

By definition of these categories, these genes are sex-biased in the respective other taxon, hence the values are already in the table. They are named as “reciprocal”.

(c) No confidence intervals are given for the alpha values, despite the legend of Figure 3 referring to them.

These were accidentally omitted - we now included the full table in suppl. Table S6; Figure 3 was modified to show violin plots of the bootstrap distributions

The author's creation and use of a "sex-bias index" (SBI). My greatest skepticism of this manuscript is with respect to the value of their manufactured index, SBI. Of course, it is possible to create such an index but does this literature really need this index or does this just add to the "clutter" in the literature for this field? Is it helping to illuminate important patterns? This index is presumably some attempt to quantify how "male-like" or "female-like" overall expression is for a given individual (for a given organ). It is calculated as SBI = (MEDIAN of all female-biased tpm) - (MEDIAN of all male-biased tpm).

(6) A main result that comes from this is that the sexes tend to overlap for these values for most nongonad tissues but are clearly distinct for gonadal tissues. I do not think this result would come as a surprise to almost anyone and I'm far from convinced that this metric is a good way to quantify that point. Let's consider testes vs. ovaries. Compared to non-gonadal tissues, I am reasonably certain that not only are there many more genes that are classified as "sex-biased" in gonads but also the magnitude of sex-bias among these genes is typically much greater than it is for the so-called sex-biased genes in nongonadal tissue (density plots requested in #3a would make this clear). In other words, males and females are, on average, very different with respect to expression in gonads so even allowing for variation within each sex will still result in a clear separation of all individuals of the two sexes. In contrast, males and females are, on average, much less different in, say, heart so when we consider the variation within each sex, there is overlap. One could imagine a variety of different metrics which could be used to make this point. The merits of "SBI" are unclear. It is a novel metric and its properties are poorly understood. (A simple alternative would be looking at individual scores along the axis separating mean/median males and females; almost certainly, for gonads, this would be very similar to PC scores for PC1.)

As throughout the text, we use gonadal comparisons only as general reference, not as the main result. The main result that we are stressing is the fast turnover of these patterns, including from binary to overlapping for kidney and liver in mouse. We consider this as a new finding. If it comes "not to a surprise to anyone", isn´t it great that one does not have to guess anymore but has finally real data on this?

We have now also added a mosaic analysis to show that the SBI can be used as summary measure in different presentations.

The use of a single PC axis is no good alternative, since it throws away the information from the other axis.

We have now included an explicit discussion on the usefulness of the SBI.

(7) For simplicity, let's assume all males are identical and all females are identical. Let's imagine that heart and kidney have the exact same set of sex-biased genes. There are 20 female-biased genes; they all happen to be identical in expression level (within tissue) and look like this:

Female TPM Male TPM TPM ratio (F:M)

Heart 4 2 2

Kidney 40 20 2

And there are 20 male-biased genes that look like this:

Female TPM Male TPM TPM ratio (F:M)

Heart 1 3 1/3

Kidney 10 30 1/3

Most people would describe these two tissues as equally sex-biased.

However, the SBIs would be:

Female SBI Male SBI Sex difference (F - M)

Heart 4-1 = 3 2 - 3 = -1 4

Kidney 40-10 =30 20-30 = -10 40

Is it a desirable property that by this metric these two tissues have wildly different SBI values for each sex as well as for the difference between sexes? (At the very least, shouldn't you make readers aware of these strange properties of SBI so they can decide how much value they put into them?)

Actually, in this example the simple ratio between the expression levels has a strange property, since it does not reflect a much higher expression of the relevant genes in the kidney. The SBI is actually more suitable for making such cases clear. Of course, this is under the assumption that expression level has a meaning for the phenotype, but this is the general assumption for all RNA-Seq experiment comparisons.

(8) With respect to Figure 4, why do females often have mean SBI values close to zero or even negative (e.g., kidney, mammary glands)? Is this simply because the female-biased genes tend to have lower TPM than the male-biased genes? It seems that the value zero for this metric is really not very biologically meaningful because this metric is a difference of two things that are not necessarily expected to be equal.

This is the extra information about the expression levels that is gained via the SBI values (see comment above). However, we noticed that people can get confused about this. We have now added a re-scaling step to focus completely on the variance information in these plots.

(9) Interpreting variances. A substantial fraction of the latter half of the manuscript focuses on interpreting variances among individual samples. This is problematic because there is no replication within individuals (i.e.., "repeatability"), thus it is impossible to infer the extent of observed variance among individuals of a given group (e.g., among females) is due to true biological differences among individuals or is simply due to noise (i.e., "measurement error" in the broad sense). Is the larger variance for mammary glands than liver or gonads just due to measurement error? What is the evidence?

This point was of course a major issue during the times where microarrays were used for transcriptome studies. However, the first systematic RNA-Seq studies showed already that the technical replicability is so high, that technical replicates are not required. In fact, practically all RNA-Seq studies are done without technical replicates for this reason.

(10) Because I have little confidence in the SBI metric (#7-8) and in interpreting within sex variances (#9), I found little value in the human results and how SBI distributions (and degree of overlap between sexes) compare between humans and mice.

We disagree - the current published status is that there are thousands of sex-biased gene in humans and this has implications for gender-specific medicine (Oliva et al. 2020). Our results show a much more nuanced picture in this respect.

(11) I found even less value in the single-cell data. It too suffers from the issues above. Further, as the authors more or less state, the data are too limited to say much of value here. It is impossible to tell to what extent the results are simply due to data limitations.

We have pointed out that it is still valuable to have them. They are good enough to exclude the possibility that only a small set of cells drives the overall pattern across an organ. We have further clarified this in the text.

(12) The code for data analysis should be posted on GitHub or some other repository.

The code for the sex-biased gene detection and analysis has been posted on GitHub (see Code availability in the manuscript).

Author response:

The following is the authors’ response to the original reviews

Public reviews:

Reviewer #1:

Weaknesses:

As this paper only uses anatomical analyses, no functional interpretations of cell function are tested.

The aim of this paper was to describe the ultrastructural organization of compound eyes in the extremely small wasp Megaphragma viggianii. The authors successfully achieved this aim and provided an incredibly detailed description of all cell types with respect to their location, volume, and dimensions. As this is the first of its kind, the results cannot easily be compared with previous work. The findings are likely to be an important reference for future work that uses similar techniques to reconstruct the eyes of other insect species. The FIB-SEM method used is being used increasingly often in structural studies of insect sensory organs and brains and this work demonstrates the utility of this method.

We thank you for your high assessment of our work. Unfortunately, it is hard to test our functional interpretations and check them with electrophysiological methods due to the extremely small size of the animal. Studies on three-dimensional ultrastructural datasets obtained using vEM have just started to appear, and we hope that a lot of data will become available for comparison in the nearest future.

Reviewer #2:

Thank you for your work and for your high assessment of our manuscript.

Reviewer #3:

Weaknesses:

The claim that the large dorsal part of the eye is the dorsal rim area (DRA), supported by anatomical data on rhabdomere geometry and connectomics in authors' earlier work, would eventually greatly benefit from additional evidence, obtained by immunocytochemical staining, that could also reveal a putative substrate for colour vision. The cell nuclei that are located in the optical path in the DRA crystalline cone have only a putative optical function, which may be either similar to pore canals in hymenopteran DRA cornea (scattering) or to photoreceptor nuclei in camera-type eyes (focussing), both explanations being mutually exclusive.

We thank the Reviewer for high assessment of our study and for detailed analysis of our manuscript. Your comments and recommendations are very valued and helped us to improve the text. We understand that immunocytochemical methods could improve our findings and supply additional evidence, but there is no technical possibility for this in present. Megaphragma is a very complicated model organism for such methods. We are currently working on the optimization of the protocol for staining, which is needed because of the high level of autoluminescence and because of insufficient penetration of dyes into the samples.

Recommendations for the authors:

Reviewer #1:

I do not have any major concerns about the content of the paper.

There are some minor spelling and grammatical errors throughout the text but these can be identified most readily using a spelling/grammar check.

We have revised the text, checked the spelling, and fixed the grammatical errors throughout the text.

I suggest consistency when referring to the capitalization of the term 'non-DRA' as it is sometimes 'Non-DRA' in the text.

We have fixed the term “non-DRA” throughout the text. Thank you.

Also, check carefully the spelling of headings in the tables as there are a few mistakes in Table 1 and 5 in particular.

The grammar errors have been fixed.

Figure 7 legend: an explanation of the abbreviation RPC should be added.

We have done so.

Reviewer #2:

(1) The paper presents the data in great detail, however, since this is the first time the technique has been applied to get whole insect eyes, even if on a small insect, it would be worth outlining in the methods section what innovations in the staining/ scanning or sample preparation allowed these improvements and a roadmap for extending this method to larger insects if possible.

The whole method, including sample preparation, staining, and scanning, was described in our previous paper (Polilov et al., 2021), where it was presented in every detail. Due to the complicated methodology we suppose that it is not necessary to include all the stages of the technique in the present paper, and thus described it more briefly.

(2) The optical modelling needs a statement in the discussion providing a disclaimer on parameters like sensitivity, anatomical measurements can provide limits and some measure, but the inherent optics are also key and it is worth qualifying these as only estimates and measurements that give a sense of the variation in morphology, only coupled with optical and potentially neural measurements could one confirm the true sensitivity and acceptance angle.

In the absence of experimental data or precise computational models of Megaphragma vision, we try to discuss rather carefully the functions of structures based on their morphology, ultrastructure, first-order visual connectome, and analogies with other species. This is reflected in the methods and those sections of our paper that contain functional interpretations.

Reviewer #3

(1) The finding that the CNS neurons are enucleated, while the compound eye contains cell nuclei, deserves another word. I would confidentially say that the optical demands of a miniaturized compound eye (the minimal size of the optics due to diffraction, the rhabdomere size, and the minimal thickness of optically insulating granules) are such that further cellular miniaturization is not possible, and the minimal sizes even render the cells that build the eye sufficiently large to accommodate cell nuclei. This is in my opinion a parsimonious explanation, yet speculative and I leave it up to you to embrace it or not.

We agree with the Reviewer and understand the limiting factors and the optical demands of a miniaturized compound eye. According to our data, nuclei occupy a considerable volume in the eye (in the cells of compound eye there are more nuclei than in the whole brain), and on average the cell volume is larger than in Trichogramma, which is minute, but larger than Megaphragma. But as the Reviewer rightly assumed, it is speculative; therefore, we would like to avoid it.

(2) Our current understanding of DRA optics and function is limited and I claim that your interpretation of the cell nuclei in the DRA dioptrical apparatuses is inappropriate. Please consider a few articles on hymenopteran DRA, starting with the one below and the citing literature:

Meyer, E.P., Labhart, T. Pore canals in the cornea of a functionally specialized area of the honey bee's compound eye. Cell Tissue Res. 216, 491-501 (1981). https://doi.org/10.1007/BF00238646

Honebyee DRA has a milky appearance under a stereomicroscope and can be discerned from the outside. This is due to pore canals in the cornea. I happen to be studying this exact structure and its function right now. I found that the result of those canals is not so much the extended receptor acceptance angles, but rather a minimized light gain. This is counterintuitive, but think of the following. The DRA photoreceptors must encode the limited range of polarization contrasts with a maximal working dynamic range (= voltage) of the photoreceptors, which results in a very steep stimulus-response curve.

Physiologically such a curve is due to very high transduction gain and a high cell input resistance. In most of the retina, small contrasts are transcoded by LMC neurons, but DRA receptors are long visual fibres and must do the job themselves. The skylight intensity (especially antisolar, where the polarized pattern is maximal) varies little during the day. Hence, the DRA receptors work almost at a fixed intensity range. In order to prevent receptor saturation and keep steep contrast coding, the corneal lenses in DRA have a built-in diffusor ring, which diminishes the light influx. Unfortunately, I have yet to publish this and I may be wrong, of course. But if I look into your data, I see consistently smaller corneal lenses and crystalline cones in the DRA, plus the cell nuclei obstructing the incident light. I think this is similar to the optics of honeybee DRA.

You do not support your claim that the nuclei additionally focus light by optical calculations, but cite literature on camera-type eyes, which is not OK.

In any case, I think it is fair to limit the discussion by saying that the nuclei may have an optical role. Further evidence from hymenopteran and vertebrate literature is controversial. “so that the nuclei act as extra collecting lenses, as was reported for rod cells of nocturnal vertebrates (Solovei et al., 2009; Błaszczak et al., 2014)” - please consider omitting this.

We thank the Reviewer for this piece of advice. And we have rewritten the text, to omit the comparison with vertebrates, but left the citation as an illustration of the fact that nuclei could perform the optical role.

“Since the nuclei in DRA and non-DRA ommatidia are arranged differently in cone cells, we suggest that the nuclei of the cone cells of DRA ommatidia in M. viggianii perform some optical role, facilitating the specialization of this group of ommatidia. The optical function for nuclei was described for rod cells of nocturnal vertebrates, where chromatin inside the cell nucleus has a direct effect on light propagation (Solovei et al., 2009; Błaszczak et al., 2014; Feodorova et al., 2020).”

(3) Please consider comparing the structure and function of ectopic receptors with the eyelet in Drosophila (i.e. https://doi.org/10.1523/JNEUROSCI.22-21-09255.2002 )

We thank the Reviewer for this advice and have included the comparison fragment into the text:

“The position of ePR, their morphology and synaptic targets look similar to the eyelet (extraretinal photoreceptor cluster) discovered in Drosophila (Helfrich-Förster et al., 2002). Eyelets are remnants of the larval photoreceptors, Bolwig’s organs in Drosophila (Hofbauer, Buchner, 1989). Unlike Drosophila, Trichogrammatidae are egg parasitoids and their central nervous system differentiation is shifted to the late larva and even early pupa (Makarova et al., 2022). According to the available data on the embryonic development of Trichogrammatidae, no photoreceptors cells were found during the larval stages (Ivanova-Kazas, 1954, 1961).”

According to this, the analogy question remains open.

(4) Minor remarks:

“but also to trace the pathways that connect the analyzer with the brain.” - I find the word analyzer a bit stretched here; sure, the DRA is polarization analyzer, but if the main retina was monochromatic, it would only be a detector, not an analyzer.

The sentence was changed according to the Reviewer’s advice.

Table I: thikness -> thickness, wigth -> width

We have fixed these misprints.

“The cross-section of Non-DRA ommatidia has a strongly spherical shape” - perhaps circular, not spherical. And not necessary to say “strongly”

The spelling was changed according to the Reviewer’s advice.

“which can be rarely visualized in the cell's projections not far from the basement membrane.” - I'd suggest saying “which are nearly absent in retinula axons”

The spelling was changed according to the Reviewer’s advice.

“The pigment granules of the retinula cells have an elongated nearly oval shape” - please consider replacing 'elongated nearly oval' with 'prolate' (try googling for “prolate” or “oblate spheroids”; the adjective describes precisely what you wanted to say)

We thank the Reviewer for this piece of advice but prefer to leave our original phrasing, because it is more readily understandable.

“The results of our morphological analysis of all ommatidia in Megaphragma are consistent with the light-polarization related features in Hymenoptera and other insects” - please add citations, see my comment on the DRA above.

We have added the citations according to the Reviewer’s advice.

“The group of short PRs (R1-R6)” - please consider renaming into “short visual fibre photoreceptors” (as opposed to “long visual fibre PRs”; hence SVFs and LVFs). This naming is quite common.

The naming was changed according to the Reviewer’s advice.

“The total rhabdom shortening in M. viggianii ommatidia probably favors polarization and absolute sensitivity,” - please see comments on DRA. Wide rhabdom means also a wider acceptance angle.

Shortening of DRA rhabdoms does not result in their widening compared to other rhabdoms, so it is difficult to say how this may be related to sensitivity. The comments on DRA given earlier have been taken into account.

“Ommatidia located across the diagonal area of the eye are more sensitive to light” - I don't understand what is diagonal area.

We have deleted the sentence.

“Estimated optical sensitivity of the eyes very close to those reported for diurnal hymenopterans with apposition eyes (Greiner et al., 2004; Gutiérrez et al., 2024) and possess around 0.19 {plus minus} 0.04 μm2 sr. M. viggianii have reasonably huge values of acceptance angle Δρ, and thus should result in a low spatial resolution” - please correct English here. “eyes IS very close”, “should result in a low”

The grammatical errors were fixed.

Table 6 legend: “SPC - secondary pigment cells.” -> “SPC – secondary pigment cells.”

Citation “(Makarova et al., 2025).” - probably 2015

The typos were fixed.

Methods, FIB-SEM: I can't understand the sentence “The volumetric data of lenses and cones, some linear measurements (lens thickness, cone length, cone width, curvature radius) and to visualize the complete 3D-model of eye we use (measure or reconstruct) the elements from another eye (left).”

The sentence is a continuation of the previous one. We have rewritten it as follows to clarify the meaning and move it to the 3D reconstruction section:

“The right eye, on which the reconstruction was performed, has several damaged regions from milling (see Appendix 1С), which hinder the complete reconstructions of lenses and cones on a few ommatidia. According to this, for the volumetric data on lenses and cones, some linear measurements (lens thickness, cone length, cone width, curvature radius), we use (measure or reconstruct) the corresponding elements from the other (left) eye.”

“The cells of single interfacet bristles were not reconstructed, because of damaging on right eye and worst quality of section on the left.” - please change to “The cells of the single interfacet bristle were not reconstructed, because of damage to the right eye and inferior quality of the sections of the left eye.”

The text has been changed as follows:

“The cells of single interfacet bristles were not reconstructed, because of the damage present in the right eye and because of the generally lower quality of this region on the left eye.”

“Morphometry. Each ommatidia was” -> “Morphometry. Each ommatidium was”

The grammatical error has been fixed.

Author response:

The following is the authors’ response to the original reviews

Reviewer #3 (Recommendations for the authors):

Major concerns:

P.6, lines 223-224: The sentence sounds like the authors produced all the OVGP1s by themselves in their laboratories, which is not completely true. The recombinant human and mouse OVGP1s were purchased from OriGene. It is suggested that the authors should state and explain clearly here which OVGP1 is produced by their laboratories and that recombinant human and mouse OVGP1s were obtained and purchased from Origene.

It is already clearly included in the M&M.

P6, lines 227-229: The authors stated that "Western blots of the three OVGP1recombinants indicated expected sizes based on those of the proteins: 75 kDa for human and murine OVGP1 and around 60 kDa for bovine OVGP1 (Fig. 4B and S6)." I pointed out in my last review report that the size of the recombinant human OVGP1shown by the authors in their manuscript is not in agreement with what has been published previously in literature regarding the molecular weight of native human OVGP1 as well as that of recombinant human OVGP1. The authors did not address the above concern adequately. In fact, recombinant human OVGP1 has been produced a few years ago (Reproduction (2016) 152:561-573) and it has been previously demonstrated that a single protein band of approximately 110-130 kDa was detected for both native human OVGP1 (see Microscopy Research and Technique (1995) 32:57-69) and recombinant human OVGP1 (Reproduction (2016) 152:561-573; Carbohydrate Research (2012) 358:47-55) using antibodies specific for human OVGP1. Molecular weight of the protein core or polypeptide of human OVGP1 is approximately 75 kDa, but the glycosylated form of native human OVGP1 and recombinant human OVGP1 is approximately 110-130 kDa. Therefore, the authors might have been using the recombinant core protein of human OVGP1 instead of the fully glycosylated recombinant OVGP1 in their study. The same concern also applies to the commercially obtained mouse recombinant OVGP1 used by the authors in their study. I would also like to mention that the mature and fully glycosylated OVGP1s in mammals vary in molecular weight (90-95 kDa in domestic animals; 110-150 kDa in primates; 160-350 kDa in rodents). Again, the 75kDa of mouse OVGP1 detected by the authors could be the core protein or polypeptide of mouse OVGP1 instead of the fully glycosylated mouse OVGP1.

In our study, as previously mentioned, we included commercially available recombinant proteins from Origene for human and murine OVGP1, which are produced in mammalian cells, and we also produced and purified bovine OVGP1 in mammalian cells. Therefore, these proteins should be properly glycosylated. Moreover, we performed Western blot assays favouring the blotting of higher molecular weight proteins, ensuring the optimal conditions for the assay. Additionally, we tested the size of OVGP1 from murine and bovine oviductal fluids on the same blot. During oestrus, the size of OVGP1 from oviductal fluids matches that of the recombinant proteins, and this band is downregulated during anoestrus, confirming the proper size of recombinant protein.

P.7, lines 236 and 237: Please provide a figure or source to support the statement "...as confirmed by proteomics of the bands along with PEAKS Studio v11.5 search engine peptide identification software."

It is included in the text the amount of unique peptides obtained by Proteomics for OVGP1 identification over all protein groups identified.

P.7, lines 243 to 245: The statement "...using rabbit polyclonal antibody to human OVGP1 for bOVGP1 and endogenous OVGP1, and mouse monoclonal antibody against Flag (DDK)-tag for hOVGP1 and mOVGP1." is confusing and might be inaccurate. First of all, I wondered why the authors did not use an antibody against bovine OVGP1 for the recombinant bOVGP1 instead of using a rabbit polyclonal antibody to human OVGP1. Secondly, what does the "endogenous OVGP1" refer to in the statement? Thirdly, the authors in their study used the commercially available recombinant human OVGP1 and recombinant mouse OVGP1 purchased from Origene. Based on the data sheet provided by Origene, the tag used for both recombinant human OVGP1 and recombinant mouse is C-Myc/DDK-tag and not Flag-tag. Can the authors explain these discrepancies?

Firstly, for the recombinant protein of bOVGP1 we used the same antibody that we used in the Western blot for all the proteins and oviductal fluids because we do not have anti-His tag working for Immunofluorescence (the one we had only worked for Western blot) and neither we do not have any antibody against bovine OVGP1. In the case of human and murine since we had anti-Flag antibody that worked for Western blot and for immunofluorescence, we used this one. However, as has been shown in our figure and supplementary material, the antibody against human OVGP1 works properly for both techniques (Western blot and Immunofluorescence). Secondly, endogenous OVGP1 is referred to the OVGP1 present in the oviductal fluid. Thirdly, as you can see in the datasheet of the protein, the recombinant proteins purchased from Origene contains a c-myc tag (EQKLISEEDL) some amino acids and a ddk-tag (DYKDDDDK). The sequence of ddk is the same of Flag-tag (DYKDDDDK). Since the proteins have both tags we used the antibody against Flag (or ddk) epitope.

P12, lines 429-432: The newly added statement at the end of the Discussion saying "Additionally, future studies would be valuable to investigate whether incubating oocytes with oviductal fluid (or OVGP1) could reduce polyspermy in porcine IVF and whether ZPs could be leveraged to naturally enhance sperm selection in human ICSI" is very concerning and requires further attention. The statement reflects that the authors do not keep pace with and do not pay attention to what has been published in literature regarding porcine and human OVGP1s. In fact, porcine oviduct-specific glycoprotein (OVGP1) has already been reported to reduce the incidence of polyspermy in pig oocytes (Biology of Reproduction (2000) 63:242-250). Porcine oviductal fluid, used in porcine IVF, has also been found to exert a beneficial effect on oocytes by reducing the incidence of polyspermy without decreasing the penetration rate. (Theriogenology (2016) 86:495-502). Therefore, the studies deemed valuable by the authors to be investigated in the future have, in fact, already been carried out two decades ago by several other laboratories. I am surprised the authors were not aware of these published work in literature. All the above should have been incorporated in the Discussion.

This sentence is modified in the discussion and the references are included.

Furthermore, as mentioned earlier, recombinant human OVGP1 has also been produced (Reproduction (2016) 152:561-573), and recombinant human OVGP1 has been found to increase tyrosine phosphorylation of sperm proteins, a biochemical hallmark of sperm capacitation, and potentiate the subsequent acrosome reaction (Reproduction (2016) 152:561-573) as well as increase sperm-zona binding (Journal of Assisted Reproduction and Genetics (2019) 36:1363-1377). These earlier findings should be incorporated into the Discussion.

Thank you for your comment, but in this work we had not performed any experimental setting related to tyrosine phosphorylation and despite is a very interesting topic is not directly related to this work.

P.19, lines 678-683: Since the human and mouse recombinant oviductin proteins were purchased from Origene, the authors should be aware of the fact that these commercially available recombinant OVGP1s might not be fully glycosylated. While I appreciate the fact that the authors wanted to briefly describe how the human and mouse recombinant OVGP1s were prepared by the manufacturer, I strongly suggest that the authors should contact Origene, the manufacturer, for all information regarding the procedures for producing the human and mouse recombinant oviductin proteins. For example, the authors stated on lines 680-681 that "A sequence expressing FLAG-tagged epitope proteins (DYKDDDDK) was cloned into an expression vector." According to the data sheet provided by Origene, it appears that both human and recombinant oviductin proteins are C-Myc/DDK-tagged and not FLAG-tagged.

Thank you for your comment, as according to the sequence of Flag-tag it is matching with the sequence of the tag in the datasheet corresponding to DDK (this is in detail in previous comment). Besides, the protein is tagged also by C-Myc tag. Among both tags, the antibody selected to detect it was anti-Flag tag.

P.19, lines 692-697: The description of the primary and secondary antibodies used for detection of the various recombinant OVGP1s is also very confusing and not clearly presented. For example, it is mentioned here that "...membranes were...incubated with anti-OVGP1 rabbit monoclonal antibody for OVGP1,..". What specifically does "OVGP1" refer to here? The authors then stated that anti-Histamine Tag antibody was used to detect bOVGP1 and mOVGP1 and anti-Flag antibody was used to detect hOVGP1. As pointed out earlier, the human and mouse recombinant OVGP1s were produced using C-Myc/DDK tag and not His-tag or Flag-tag. Can the authors clarify these discrepancies?

We apologise for the complexity of the antibodies, we included in this paragraph the ones used to Western blot for both figures: anti- human OVGP1 was used for the principal figure that contains the three recombinant proteins and oviductal fluids; and the anti-Histidine and anti-Flag antibodies that are included in supplementary figure, specifically for recombinant bovine OVGP1 (Histidine tag) and for recombinant murine and human OVGP (DDK tag). A clarifying sentence has been included in the text.

P.31, lines 1143-1149: Figure 10 is not mentioned anywhere in the main text of the manuscript. Rewrite the second half of the sentence "...; being this specificity lost when OVGP1 is heterologous to the ZP (right diagram)." Which sounds awkward and grammatically not correct.

The figure is already mentioned in the text, thank you for your comment. The sentence is also corrected.

Other comments: P.1, the statement of "All authors contributed equally to this work" on line 14 can be deleted because detailed and specific contributions from each authors are listed in lines 1009-1017 on page 27.

Both authors contributed equally to this work, now is clear in authors contribution section.

P.2, lines 43 and 44: Do the authors mean "sperm-oocyte binding protein" instead of "sperm-oocyte fusion protein" in the sentence? "Fusion protein" is a protein composed of two or more domains encoded by different genes, or a hybrid molecule created by combining two different proteins for various purposes. I believe the term "fusion protein" is wrongly used in the sentence which should be rephrased with a proper term.

Done.

P2, line 73: Remove the comma after the word "Both".

Done.

P.5, line 179: "...mice ZP..." should be written as "...mouse ZP...".  

Done.

P.6, heading of 3rd paragraph on line 207: The term "binding" will be a better term than "fusion" used in the heading because the results do not actually show the fusion of the OVGP1 proteins with the ZP glycoprotein. Instead, binding of the OVGP1 proteins to the ZP occurred.

Done.

P.6, lines 215-217: Authors, please provide a reference or references to support the statement "Region A, corresponding to the amino acid end, shows high identity among monotremes, marsupials and placentals."

In the text was indicated a review (29) which includes the supporting idea of this statement for Figure 4. Moreover, we have included some if the references used for the description of the domains when performing the sequence alignment of Figure S5.

P.6, line 230 and line 233 on P.7: Authors, please be consistent in the use of either American English or British English. The word "oestrus" is British English whereas "estrus" is American English.

Done.

P.7, line 264: The word "sticking" used here means non-specific binding. I believe the author means specific binding here. If so, a more appropriate word should be used here instead of "sticking".

Done.

P.7, lines 267-269: This newly added sentence sounds very awkward and should be completely rewritten.

Done.

P.8, line 288: This reviewer finds it difficult to understand the meaning of the heading. The heading should be rephrased to bring out exactly what the authors want to say in well-written English.

Done.

P.8, line 290: The word "would" should be replaced by "could" in the sentence.

Done.

P.13, line 437: Authors, please provide the location of Sigma-Aldrich.

Done.

P.13, line 457: Here, the authors used "1800 rpm" to indicate the centrifugation speed but used the g-force elsewhere in the Materials and Methods. Please be consistent. The g-force is preferred.

Done.

P.14, lines 483-485: The procedure of sacrificing the cats should be provided in the Materials and Methods

Cats weren’t sacrificed they were vasectomized. It is now included in the text.

P.17, line 628: "...the ZPs were exposed or no exposed to..." should be written as "...the ZPs were either exposed or not exposed to...".

Done.

P.17, line 629: "...each groups were incubated with..." should be "...each group was incubated with...".

Done.

P.19, line 700: "As loading control, was used the primary antibody....." is not a complete sentence and it needs to be rewritten.

Done.

P.20, lines 744-754: For scanning electron microscopy and image processing, the procedures of prior treatment of the oocytes with and without oviductal fluid and OVGP1 should be included here.

Done.

P.21, line 756: It is stated here that "Two hundred isolated ZPs were treated with Clostridium perfringens neuraminidase....". However, it is not clear whether two hundred isolated ZPs of both porcine and murine ZPs were treated. Authors, please clarify.

We used 200 isolated ZPs of each specie, bovine and murine. It is classified in the text.

P.28, lines 1039 and 1040: The author only mentioned the use of bovine and murine sperm here. What about human sperm?

Done.

P.29, line 1076: "...in mammalian cells..." is very vague. Be specific what exactly the mammalian cells were.

Done.

P.29, line 1079: "Oviductal fluid from ovulated cows or anoestrus cows." is not a complete sentence and it needs to be rewritten.

Done.

Author response:

Conflation of control, difficulty and reward rate

In response to the comment of control being conflated with task difficulty (and thus reward rate) that the reviewer feels is not adequately discussed in the paper, we will add more to this point in our discussion, especially in relation to previous literature. It is important to note, however, that our measure of perceived difficulty was included in analyses assessing the fluctuations in stress and control. Subjective control still had a unique effect on the experience of stress over and above perceived difficulty, suggesting that subjective control explains variance in stress beyond what is accounted for by perceived difficulty. We will also include additional analyses in which we include the win rate (i.e. percentage of all trials won) as a covariate when assessing the relationship between subjective control, perceived difficulty and subjective stress, which shows that win rate does not predict stress, but subjective control and perceived difficulty still uniquely predict subjective stress. The results of this will be added and elaborated further in the discussion.

Neutral video condition

In response to the comment of the neutral video condition not being active enough, we believe that any task with action-outcome contingencies would have a degree of controllability. To better distinguish experiences of control (WS task) to an experience of no/neutral control (i.e., neither high nor low controllability), we decided to use a task in which no actions were required during the task itself, although concentration was still required (attention checks regarding the content of the videos and ratings of the videos).

The suggestion of having a high arousal video condition would indeed be interesting to test how experiencing ‘neutral’ control and high(er) stress levels preceding the stressor task influences stress buffering and stress relief. This is a good suggestion for future work that we can include in the discussion section.

The TSST version (online and anticipatory)

We will add more information regarding prior literature that the Trier Social Anticipatory Stress test has found physiological and psychological correlates (e.g. Nasso et al., 2019, Schlatter et al., 2021, Steinbeis et al., 2015), suggesting that the anticipation is still a valid stress manipulation despite participants not performing the actual speech task. Further, the TSST had a significant impact on subjective stress in the expected direction demonstrating that it was effective at eliciting subjective stress.

Internal consistency

We will parcellate the timepoints differently (not just odd/even sliders) to test the internal consistency, for example a random split or first half/second half.

Effect of win-loss domain in Study 2

We will run additional analyses testing the interaction of Domain (win or loss) with stressor intensity when predicting the stress buffering and stress relief effects. To test whether the loss domain is more valuable at mitigating experiences of stress than the win condition, we will run additional analyses with just the high control conditions (WS task) to test for a Domain*Time interaction, as we cannot test a Control*Domain*Time interaction in the full model given that we do not have ‘Domain’ for the video (neutral control) condition.

Stress relief analyses

Regarding the stress relief analyses (timepoints 2 and 3) and ‘baseline’ stress (timepoint 1), we will add to the manuscript that there is no significant difference in stress ratings between the high control and neutral control (collapsed across stress and domain) after the WS/video task, hence why we do not think it’s necessary to include in the stress relief model. Nevertheless, we will include a sensitivity analysis in the supplementary material to test the Timepoint*Control interaction (of stress relief – timepoints 2 and 3) when including timepoint 1 stress as a covariate.

Clarity

We will add more clarity in the methods section regarding within- and between-subject manipulations. We will also add Figure S4 to the main manuscript and expand Figure 1 to include both Studies 1 and 2 and a timeline of when subjective stress was assessed throughout the experiment.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

Busch and Hansel present a morphological and histological comparison between mouse and human Purkinje cells (PCs) in the cerebellum. The study reveals species- specific differences that have not previously been reported despite numerous observations of these species. While mouse PCs show morphological heterogeneity and occasional multi-innervation by climbing fibers (CFs), human PCs exhibit a widespread, multi-dendritic structure that exceeds expectations based on allometric scaling. Specifically, human PCs are significantly larger, and exhibit increased spine density, with a unique cluster-like morphology not found in mice.

Strengths:

The manuscript provides an exceptionally detailed analysis of PC morphology across species, surpassing any prior publication. Major strengths include a systematic and thorough methodology, rigorous data analysis, and clear presentation of results. This work is likely to become the go-to resource for quantitation in this field. The authors have largely achieved their aims, with the results effectively supporting their conclusions.

We are grateful to this reviewer for their thoughtful assessment that this work will be a go-to resource for the field.

Weaknesses:

There are a few concerns that need to be addressed, specifically related to details of the methodology as well as data interpretation based on the limits of some experimental approaches. Overall, these weaknesses are minor.

We thank this reviewer for their careful reading of the manuscript and for highlighting limitations and weaknesses in the methodology. We are in full agreement that while interpretation is somewhat limited, there is still value in their description. As detailed below in response to this reviewer’s recommendations, we provide more description of our imaging resolution. This additional detail clarifies that our quantitation is appropriate for the scale of the objects being measured and provides critical information to help readers assess the findings as they may pertain to their own work.

Reviewer #2 (Public review):

Summary:

This manuscript aims to follow up on a previously published paper (Busch and Hansel 2023) which proposed that the morphological variation of dendritic bifurcation in Purkinje cells in mice and humans is indicative of the number of climbing fiber inputs, with dendritic bifurcation at the level of the soma resulting in a proportion of these neurons being multi-innervated. The functional and anatomical climbing fiber data was obtained solely from mice since all human tissue was embalmed and fixed, and the extension of these findings to human Purkinje cells was indirect. The current comparative anatomy study aims to resolve this question in human tissue more directly and to further analyse in detail the properties of adult human Purkinje cell dendritic morphology.

Strengths:

The authors have carried out a meticulous anatomical quantification of human Purkinje cell dendrites, in tissue preparations with a better signal-to-noise ratio than their previous study, comparing them with those from mice. Importantly, they now present immunolabelling results that trace climbing fiber axons innervating human PCs. As well as providing detailed analyses of spine properties and interesting new findings of human PC dendritic length and spine types, the work confirms that human PCs that have two clearly distinct dendritic branches have an approximately x% chance of receiving more than one CF input, segregated across the two branches. Albeit entirely observational, the data will be of widespread interest to the cerebellar field, in particular, those building computational models of Purkinje cells.

We thank this reviewer for their positive and considered assessment of our work. We enthusiastically agree that while these data are descriptive in nature, they may be of interest across modalities of cerebellar research and will provide a more detailed framework for cross-species comparisons and single cell computational modeling, which remains a critical tool to explore the human case given the inaccessibility of physiological experimentation.

Weaknesses:

The work is, by necessity, purely anatomical. It remains to be seen whether there are any functional differences in ion channel expression or functional mapping of granule inputs to human PCs compared with the mouse that might mitigate the major differences in electronic properties suggested.

We are in full agreement with the reviewer that the focused anatomical description of this manuscript could not make strong assertions about function given that cellular and circuit physiology is determined by many additional factors that remain unexamined. We appreciate that the reviewer acknowledges that this is out of necessity as those factors are inaccessible to experimentation at the current time; however, we are enthusiastic that our current findings will motivate future work that will shed light on these critical additional features of the system, both in rodents and humans.

Reviewer 1 (Recommendations for the authors):

PCs are now known to be genetically diverse, with unique PC types found only in humans. Could this cellular diversity contribute to the differences observed between species in this study? This possibility should be at least discussed in the context of the findings.

We agree that this is a fascinating possibility. The perhaps most detailed recent study (Sepp et al., Nature 625, 2024) – in a conservative assessment – describes four developmental PC subtypes in mice that are identical in humans. The study points out that the subtype ratio changes over the course of development, though. Taken together with the possibility of additional human-specific subtypes, a genetic basis for morphological as well as physiological diversity arises. This is now discussed on p. 7. It needs to be kept in mind, however, that other factors, such as push-pull influences during tissue growth, might also play a role.

The human tissue used in this study was obtained from elderly individuals, while the mouse tissue was not. It is unclear whether the age difference might influence the findings, and this warrants further discussion or control.

We share this concern, in particular regarding the spine / spine cluster analysis as here tissue quality and or degenerative effects might play a role. We additionally analyzed a tissue sample from a 37 year-old human, and observed the same spine clusters as in the other human brains. This is now described on p. 4 of the revised manuscript.

The study includes spine size comparisons, but it is not clear if the point spread function (PSF) of the microscope provides the necessary resolution for these quantitative assessments. For instance, are multi-headed spines truly multi-headed, or could this be an artifact of limited resolution?

This is an important point. We addressed it by calculating the Rayleigh limit (more conservative than the Abbe limit) as 248.4nm for the equipment and conditions used (Methods, p. 22). On pages 3-5, we updated our Results section accordingly to point out what quantifications are well supported and discuss the limitations (p. 3-5).

Reviewer 2 (Recommendations for the authors):

This is nice work which must have been very time-consuming. It would be good to make sure that the technical details are properly discussed, to quantify the data properly. Please include details of how you measured the resolution of the microscope used to evaluate spine size.

See our response to the last comment of Referee 1 above.

The figure panels are mostly satisfactory, but they are exceptionally crowded and will probably be difficult to read at the final size. Some work tidying these would be worth it. In Figure 3B, include mention of open and blue triangles in legend. In 3E, the dendritic branches are shown at a different gray scale. You have not done this elsewhere, so probably good to mention it in the legend.

Figure 3 and its legend have been updated / improved accordingly.

The definition of horizontal and vertical is not absolutely clear. Perhaps re-assess this bit of the text. Does it mean that you did not include cells that were neither vertical nor horizontal?

We categorized those PCs as ‘vertical’ that have a >30° angle relative to the PC layer, and those as ‘horizontal’ that have a <30° angle relative to the PC layer. All PCs are covered by these categories. This is now described on p. 5.

Author response:

The following is the authors’ response to the original reviews

We extend our sincere thanks to the editor, referees for eLife, and other commentators who have written evaluations of this manuscript, either in whole or in part. Sources of these comments were highly varied, including within the bioRxiv preprint server, social media (including many comments received on X/Twitter and some YouTube presentations and interviews), comments made by colleagues to journalists, and also some reviews of the work published in other academic journals. Some of these are formal and referenced with citations. Others were informal but nonetheless expressed perspectives that helped enable us to revise the manuscript with the inclusion of broader perspectives than the formal review process. It is beyond the scope of this summary to list every one of these, which have often been brought to the attention of different coauthors, but we begin by acknowledging the very wide array of peer and public commentary that have contributed to this work. The reaction speaks to a broad interest in open discussion and review of preprints. 

As we compiled this summary of changes to the manuscript, we recognized that many colleagues made comments about the process of preprint dissemination and evaluation rather than the data or analyses in the manuscript. Addressing such comments is outside the scope of this revised manuscript, but we do feel that a broader discussion of these comments would be valuable in another venue. Many commentators have expressed confusion about the eLife system of evaluation of preprints, which differs from the editorial acceptance or rejection practiced in most academic journals. As authors in many different nations, in varied fields, and in varied career stages, we ourselves are still working to understand how the academic publication landscape is changing, and how best to prepare work for new models of evaluation and dissemination. 

The manuscript and coauthor list reflect an interdisciplinary collaboration. Analyses presented in the manuscript come from a wide range of scientific disciplines. These range from skeletal inventory, morphology, and description, spatial taphonomy, analysis of bone fracture patterns and bone surface modifications, sedimentology, geochemistry, and traditional survey and mapping. The manuscript additionally draws upon a large number of previous studies of the Rising Star cave system and the Dinaledi Subsystem, which have shaped our current work. No analysis within any one area of research stands alone within this body of work: all are interpreted in conjunction with the outcomes of other analyses and data from other areas of research. Any single analysis in isolation might be consistent with many different hypotheses for the formation of sediments and disposition of the skeletal remains. But testing a hypothesis requires considering all data in combination and not leaving out data that do not fit the hypothesis. We highlight this general principle at the outset because a number of the comments from referees and outside specialists have presented alternative hypotheses that may arguably be consistent with one kind of analysis that we have presented, while seeming to overlook other analyses, data, or previous work that exclude these alternatives. In our revision, we have expanded all sections describing results to consider not only the results of each analysis, but how the combination of data from different kinds of analysis relate to hypotheses for the deposition and subsequent history of the Homo naledi remains. We address some specific examples and how we have responded to these in our summary of changes below. 

General organization

The referee and editor comments are mostly general and not line-by-line questions, and we have compiled them and treated them as a group in this summary of changes, except where specifically noted. 

The editorial comments on the previous version included the suggestion that the manuscript should be reorganized to test “natural” (i.e. noncultural) hypotheses for the situations that we examine. The editorial comment suggested this as a “null hypothesis” testing approach. Some outside comments also viewed noncultural deposition as a null hypothesis to be rejected. We do not concur that noncultural processes should be construed as a null hypothesis, as we discuss further below. However, because of the clear editorial opinion we elected to revise the manuscript to make more explicit how the data and analyses test noncultural depositional hypotheses first, followed by testing of cultural hypotheses. This reorganization means that the revised manuscript now examines each hypothesis separately in turn. 

Taking this approach resulted in a substantial reorganization of the “Results” section of the manuscript. The “Results” section now begins with summaries of analyses and data conducted on material from each excavation area. After the presentation of data and analyses from each area, we then present a separate section for each of several hypotheses for the disposition and sedimentary context of the remains. These hypotheses include deposition of bodies upon a talus (as hypothesized in some previous work), slow sedimentary burial on a cave floor or within a natural depression, rapid burial by gravity-driven slumping, and burial of naturally mummified remains. We then include sections to test the hypothesis of primary cultural burial and secondary cultural burial. This approach adds substantial length to the Results. While some elements may be repeated across sections, we do consider the new version to be easier to take piece by piece for a reader trying to understand how each hypothesis relates to the evidence. 

The Results section includes analyses on several different excavation areas within the Dinaledi Subsystem. Each of these presents somewhat different patterns of data. We conceived of this manuscript combining these distinct areas because each of them provides information about the formation history of the Homo naledi-associated sediments and the deposition of the Homo naledi remains. Together they speak more strongly than separately. In the previous version of the manuscript, two areas of excavation were considered in detail (Dinaledi Feature 1 and the Hill Antechamber Feature), with a third area (the Puzzle Box area) included only in the Discussion and with reference to prior work. We now describe the new work undertaken after the 2013-2014 excavations in more detail. This includes an overview of areas in the Hill Antechamber and Dinaledi Chamber that have not yielded substantial H. naledi remains and that thereby help contextualize the spatial concentration of H. naledi skeletal material. The most substantial change in the data presented is a much expanded reanalysis of the Puzzle Box area. This reanalysis provides greater clarity on how previously published descriptions relate to the new evidence. The reanalysis also provides the data to integrate the detailed information on bone identification fragmentation, and spatial taphonomy from this area with the new excavation results from the other areas. 

In addition to Results, the reorganization also affected the manuscript’s Introduction section. Where the previous version led directly from a brief review of Pleistocene burial into the description of the results, this revised manuscript now includes a review of previous studies of the Rising Star cave system. This review directly addresses referee comments that express some hesitation to accept previous results concerning the structure and formation of sediments, the accessibility of the Dinaledi Subsystem, the geochronological setting of the H. naledi remains, and the relation of the Dinaledi Subsystem to nearby cave areas. Some parts of this overview are further expanded in the Supplementary Information to enable readers to dive more deeply into the previous literature on the site formation and geological configuration of the Rising Star cave system without needing to digest the entirety of the cited sources. 

The Discussion section of the revised manuscript is differentiated from Results and focuses on several areas where the evidence presented in this study may benefit from greater context. One new section addresses hypothesis testing and parsimony for Pleistocene burial evidence, which we address at greater length in this summary below. The majority of the Discussion concerns the criteria for recognizing evidence for burial as applied in other studies. In this research we employ a minimal definition but other researchers have applied varied criteria. We consider whether these other criteria have relevance in light of our observations and whether they are essential to the recognition of burial evidence more broadly. 

Vocabulary

We introduce the term “cultural burial” in this revised manuscript to refer to the burial of dead bodies as a mortuary practice. “Burial” as an unmodified term may refer to the passive covering of remains by sedimentary processes. Use of the term “intentional burial” would raise the question of interpreting intent, which we do not presume based on the evidence presented in this research. The relevant question in this case is whether the process of burial reflects repeated behavior by a group. As we received input from various colleagues it became clear that burial itself is a highly loaded term. In particular there is a common assumption within the literature and among professionals that burial must by definition be symbolic. We do not take any position on that question in this manuscript, and it is our hope that the term “cultural burial” may focus the conversation around the extent that the behavioral evidence is repeated and patterned. 

Sedimentology and geochemistry of Dinaledi Feature 1

Reviewer 4 provided detailed comments on the sedimentological and geochemical context that we report in the manuscript. One outside review (Foecke et al. 2024) included some of the points raised by reviewer 4, and additionally addressed the reporting of geochemical and sedimentological data in previous work that we cite. 

To address these comments we have revised the sedimentary context and micromorphology of sediments associated with Dinaledi Feature 1. In the new text we demonstrate the lack of microstratigraphy (supported by grain size analysis) in the unlithified mud clast breccia (UMCB), while such a microstratigraphy is observed in the laminated orange-red mudstones

(LORM) that contribute clasts to the UMCB. Thus, we emphasize the presence and importance

of a laterally continuous layer of LORM nature occurring at a level that appears to be the maximum depth of fossil occurrence. This layer is severely broken under extensive accumulation of fossils such as Feature 1 and only evidenced by abundant LORM clasts within and around the fossils. 

We have completely reworked the geochemical context associated with Feature 1 following the comments of reviewer 4. We described the variations and trends observed in the major oxides separate from trace and rare-earth elements. We used Harker variations plots to assess relationships between these element groups with CaO and Zn, followed by principal component analysis of all elements analyzed. The new geochemical analysis clearly shows that Feature 1 is associated with localized trace element signatures that exist in the sediments only in association with the fossil bones, which suggests lack of postdepositional mobilization of the fossils and sediments. We additionally have included a fuller description of XRF methods. 

To clarify the relation of all results to the features described in this study, we removed the geochemical and sedimentological samples from other sites within the Dinaledi Subsystem. These localities within the fissure network represent only surface collection of sediment, as no excavation results are available from those sites to allow for comparison in the context of assessing evidence of burial. These were initially included for comparison, but have now been removed to avoid confusion.  

Micromorphology of sediments

Some referees (1, 3, and 4) and other commentators (including Martinón-Torres et al. 2024) have suggested that the previous manuscript was deficient due to an insufficient inclusion of micromorphological analysis of sediments. Because these commentators have emphasized this kind of evidence as particularly important, we review here what we have included and how our revision has addressed this comment. Previous work in the Dinaledi Chamber (Dirks et al., 2015; 2017) included thin section illustrations and analysis of sediment facies, including sediments in direct association with H. naledi remains within the Puzzle Box area. The previous work by Wiersma and coworkers (2020) used micromorphological analysis as one of several approaches to test the formation history of Unit 3 sediments in the Dinaledi Subsystem, leading to the interpretation of autobrecciation of earlier Unit 1 sediment. In the previous version of this manuscript we provided citations to this earlier work. The previous manuscript also provided new thin section illustrations of Unit 3 sediment near Dinaledi Feature 1 to place the disrupted layer of orange sediment (now designated the laminated orange silty mudstone unit) into context. 

In the new revised manuscript we have added to this information in three ways. First, as noted above in response to reviewer 4, we have revised and added to our discussion of

micromorphology within and adjacent to the Dinaledi Feature 1. Second, we have included more discussion in the Supplementary Information of previous descriptions of sediment facies and associated thin section analysis, with illustrations from prior work (CC-BY licensed) brought into this paper as supplementary figures, so that readers can examine these without following the citations. Third, we have included Figure 10 in the manuscript which includes six panels with microtomographic sections from the Hill Antechamber Feature. This figure illustrates the consistency of sub-unit 3b sediment in direct contact with H. naledi skeletal material, including anatomically associated skeletal elements, with previous analyses that demonstrate the angular outlines and chaotic orientations of LORM clasts. It also shows density contrasts of sediment in immediate contact with some skeletal elements, the loose texture of this sediment with air-filled voids, and apparent invertebrate burrowing activity. To our knowledge this is the first application of microtomography to sediment structure in association with a Pleistocene burial feature. 

To forestall possible comments that the revised manuscript does not sufficiently employ micromorphological observations, or that any one particular approach to micromorphology is the standard, we present here some context from related studies of evidence from other research groups working at varied sites in Africa, Europe, and Asia. Hodgkins et al. (2021) noted: “Only a handful of micromorphological studies have been conducted on human burials and even fewer have been conducted on suspected burials from Paleolithic or hunter-gatherer contexts.” In that study, one supplementary figure with four photomicrographs of thin sections of sediments was presented. Interpretation of the evidence for a burial pit by Hodgkins et al. (2021) noted the more open microstructure of sediment but otherwise did not rely upon the thin section data in characterizing the sediments associated with grave fill. Martinón-Torres et al. (2021) included one Extended Data figure illustrating thin sections of sediments and bone, with two panels showing sediments (the remainder showing bone histology). The micromorphological analysis presented in the supplementary information of that paper was restricted to description of two microfacies associated with the proposed “pit” in that study. That study did carry out microCT scanning of the partially-prepared skeletal remains but did not report any sediment analysis from the microtomographic results. Maloney et al. (2022) reported no micromorphological or thin section analysis. Pomeroy et al. (2020a) included one illustration of a thin section; this study may be regarded as a preliminary account rather than a full description of the work undertaken. Goldberg et al. (2017) analyzed the geoarchaeology of the Roc de Marsal deposits in which possible burial-associated sediments had been fully excavated in the 1960s, providing new morphological assessments of sediment facies; the supplementary information to this work included five scans (not microscans) of sediment thin sections and no microphotographs. Fewlass et al. (2023) presented no thin section or micromorphological illustrations or methods. In summary of this research, we note that in one case micromorphological study provided observations that contributed to the evidence for a pit, in other cases micromorphological data did not test this hypothesis, and many researchers do not apply micromorphological techniques in their particular contexts. 

Sediment micromorphology is a growing area of research and may have much to provide to the understanding of ancient burial evidence as its standards continue to develop (Pomeroy et al. 2020b). In particular microtomographic analysis of sediments, as we have initiated in this study, may open new horizons that are not possible with more destructive thin-section preparation. In this manuscript, the thin section data reveals valuable evidence about the disruption of sediment structure by features within the Dinaledi Chamber, and microtomographic analysis further documents that the Hill Antechamber Feature reflects similar processes, in addition to possible post-burial diagenesis and invertebrate activity. Following up in detail on these processes will require further analysis outside the scope of this manuscript. 

Access into the Dinaledi Subsystem

Reviewer 1 emphasizes the difficulty of access into the Dinaledi Subsystem as a reason why the burial hypothesis is not parsimonious. Similar comments have been made by several outside commentators who question whether past accessibility into the Dinaledi Subsystem may at one time have been substantially different from the situation documented in previous work. Several pieces of evidence are relevant to these questions and we have included some discussion of them in the Introduction, and additionally include a section in the Supplementary Information (“Entrances to the cave system”) to provide additional context for these questions. Homo naledi remains are found not only within the Dinaledi Subsystem but also in other parts of the cave system including the Lesedi Chamber, which is similarly difficult for non-expert cavers to access. The body plan, mass, and specific morphology of H. naledi suggest that this species would be vastly more suited to moving and climbing within narrow underground passages than living people. On this basis it is not unparsimonious to suggest that the evidence resulted from H. naledi activity within these spaces. We note that the accessibility of the subsystem is not strictly relevant to the hypothesis of cultural burial, although the location of the remains does inform the overall context which may reflect a selection of a location perceived as special in some way. 

Stuffing bodies down the entry to the subsystem

Reviewer 3 suggests that one explanation for the emplacement of articulated remains at the top of the sloping floor of the Hill Antechamber is that bodies were “stuffed” into the chute that comprises the entry point of the subsystem and passively buried by additional accumulation of remains. This was one hypothesis presented in earlier work (Dirks et al. 2015) and considered there as a minimal explanation because it did not entail the entry of H. naledi individuals into the subsystem. The further exploration (Elliott et al. 2021) and ongoing survey work, as well as this manuscript, all have resulted in data that rejects this hypothesis. The revised manuscript includes a section in the results “Deposition upon a talus with passive burial” that examines this hypothesis in light of the data. 

Recognition of pits

Referee 3 and 4 and several additional commentators have emphasized that the recognition of pit features is necessary to the hypothesis of burial, and questioned whether the data presented in the manuscript were sufficient to demonstrate that pits were present. We have revised the manuscript in several ways to clarify how all the different kinds of evidence from the subsystem test the hypothesis that pits were present. This includes the presentation of a minimal definition of burial to include a pit dug by hominins, criteria for recognizing that a pit was present, and an evaluation of the evidence in each case to make clear how the evidence relates to the presence of a pit and subsequent infill. As referee 3 notes, it can be challenging to recognize a pit when sediment is relatively homogeneous. This point was emphasized in the review by Pomeroy and coworkers (2020b), who reflected on the difficulty seeing evidence for shallow pits constructed by hominins, and we have cited this in the main text. As a result, the evidence for pits has been a recurrent topic of debate for most Pleistocene burial sites. However in addition to the sedimentological and contextual evidence in the cases we describe, the current version also reflects upon other possible mechanisms for the accumulation of bones or bodies. The data show that the sedimentary fill associated with the H. naledi remains in the cases we examine could not have passively accumulated slowly and is not indicative of mass movement by slumping or other high-energy flow. To further put these results into context, we added a section to the Discussion that briefly reviews prior work on distinguishing pits in Pleistocene burial contexts, including the substantial number of sites with accepted burial evidence for which no evidence of a pit is present. 

Extent of articulation and anatomical association

We have added significantly greater detail to the descriptions of articulated remains and orientation of remains in order to describe more specifically the configuration of the skeletal material. We also provide 14 figures in main text (13 of them new) to illustrate the configuration of skeletal remains in our data. For the Puzzle Box area, this now includes substantial evidence on the individuation of skeletal fragments, which enables us to illustrate the spatial configuration of remains associated with the DH7 partial skeleton, as well as the spatial position of fragments refitted as part of the DH1, DH2, DH3, and DH4 crania. For Dinaledi Feature 1 and the Hill Antechamber Feature we now provide figures that key skeletal parts as identified, including material that is unexcavated where possible, and a skeletal part representation figure for elements excavated from Dinaledi Feature 1. 

Archaeothanatology

Reviewer 2 suggests that a greater focus on the archaeothanatology literature would be helpful to the analysis, with specific reference to the sequence of joint disarticulation, the collapse of sediment and remains into voids created by decomposition, and associated fragmentation of the remains. In the revised manuscript we have provided additional analysis of the Hill Antechamber Feature with this approach in mind. This includes greater detail and illustration of our current hypothesis for individuation of elements. We now discuss a hypothesis of body disposition, describe the persistent joints and articulation of elements, and examine likely decomposition scenarios associated with these remains. Additionally, we expand our description and illustration of the orientation of remains and degree of anatomical association and articulation within Dinaledi Feature 1. For this feature and for the Hill Antechamber Feature we have revised the text to describe how fracturing and crushing patterns are consistent with downward pressure from overlying sediment and material. In these features, postdepositional fracturing occurred subsequent to the decomposition of soft tissue and partial loss of organic integrity of the bone. We also indicate that the loss by postdepositional processes of most long bone epiphyses, vertebral bodies, and other portions of the skeleton less rich in cortical bone, poses a challenge for testing the anatomical associations of the remaining elements. This is a primary reason why we have taken a conservative approach to identification of elements and possible associations. 

A further aspect of the site revealed by our analysis is the selective reworking of sediments within the Puzzle Box area subsequent to the primary deposition of some bodies. The skeletal evidence from this area includes body parts with elements in anatomical association or articulation, juxtaposed closely with bone fragments at varied pitch and orientation. This complexity of events evidenced within this area is a challenge for approaches that have been developed primarily based on comparative data from single-burial situations. In these discussions we deepen our use of references as suggested by the referee.   

Burial positions

Reviewer 2 further suggests that illustrations of hypothesized burial positions would be valuable. We recognize that a hypothesized burial position may be an appealing illustration, and that some recent studies have created such illustrations in the context of their scientific articles. However such illustrations generally include a great deal of speculation and artist imagination, and tend to have an emotive character. We have added more discussion to the manuscript of possible primary disposition in the case of the Hill Antechamber Feature as discussed above. We have not created new illustrations of hypothesized burial positions for this revision. 

Carnivore involvement

Referee 1 suggests that the manuscript should provide further consideration of whether carnivore activity may have introduced bones or bodies into the cave system. The reorganized Introduction now includes a review of previous work, and an expanded discussion within the Supplementary Information (“Hypotheses tested in previous work”). This includes a review of literature on the topic of carnivore accumulation and the evidence from the Dinaledi and Lesedi Chamber that rejects this hypothesis. 

Water transport and mud

The eLife referees broadly accepted previous work showing that water inundation or mass flow of water-saturated sediment did not occur within the history of Unit 2 and 3 sediments, including those associated with H. naledi remains. However several outside commentators did refer specifically to water flow or mud flow as a mechanism for slumping of deposits and possible sedimentary covering of the remains. To address these comments we have added a section to the

Supplementary Information (“Description of the sedimentary deposits of the Dinaledi Subsystem”) that reviews previous work on the sedimentary units and formation processes documented in this area. We also include a subsection specifically discussing the term “mud” as used in the description of the sedimentology within the system, as this term has clearly been confusing for nonspecialists who have read and commented on the work. We appreciate the referees’ attention to the previous work and its terminology.  

Redescription of areas of the cave system

Reviewer 1 suggests that a detailed reanalysis of all portions of the cave system in and around the Dinaledi Subsystem is warranted to reject the hypothesis that bodies entered the space passively and were scattered from the floor by natural (i.e. noncultural) processes. The referee suggests that National Geographic could help us with these efforts. To address this comment we have made several changes to the manuscript. As noted above, we have added material in Supplementary Information to review the geochronology of the Dinaledi Subsystem and nearby Dragon’s Back Chamber, together with a discussion of the connections between these spaces. 

Most directly in response to this comment we provide additional documentation of the possibility of movement of bodies or body parts by gravity within the subsystem itself. This includes detailed floor maps based on photogrammetry and LIDAR measurement, where these are physically possible, presented in Figures 2 and 3. In some parts of the subsystem the necessary equipment cannot be used due to the extremely confined spaces, and for these areas our maps are based on traditional survey methods. In addition to plan maps we have included a figure showing the elevation of the subsystem floor in a cross-section that includes key excavation areas, showing their relative elevation. All figures that illustrate excavation areas are now keyed to their location with reference to a subsystem plan. These data have been provided in previous publications but the visualization in the revised manuscript should make the relationship of areas clear for readers. The Introduction now includes text that discusses the configuration of the Hill Antechamber, Dinaledi Chamber, and nearby areas, and also discusses the instances in which gravity-driven movement may be possible, at the same time reviewing that gravity-driven movement from the entry point of the subsystem to most of the localities with hominin skeletal remains is not possible. 

Within the Results, we have added a section on the relationship of features to their surroundings in order to assist readers in understanding the context of these bone-bearing areas and the evidence this context brings to the hypothesis in question. We have also included within this new section a discussion of the discrete nature of these features, a question that has been raised by outside commentators. 

Passive sedimentation upon a cave floor or within a natural depression

Reviewer 3 suggests that the situation in the Dinaledi Subsystem may be similar to a European cave where a cave bear skeleton might remain articulated on a cave floor (or we can add, within a hollow for hibernation), later to be covered in sediment. The reviewer suggests that articulation is therefore no evidence of burial, and suggests that further documentation of disarticulation processes is essential to demonstrating the processes that buried the remains. We concur that articulation by itself is not sufficient evidence of cultural burial. To address this comment we have included a section in the Results that tests the hypothesis that bodies were exposed upon the cave floor or within a natural depression. To a considerable degree, additional data about disarticulation processes subsequent to deposition are provided in our reanalysis of the Puzzle Box area, including evidence for selective reworking of material after burial. 

Postdepositional movement and floor drains

Reviewer 3 notes that previous work has suggested that subsurface floor drains may have caused some postdepositional movement of skeletal remains. The hypothesis of postdepositional slumping or downslope movement has also been discussed by some external commentators (including Martinón-Torres et al. 2024). We have addressed this question in several places within the revised manuscript. As we now review, previous discussion of floor drains attempted to explain the subvertical orientation of many skeletal elements excavated from the Puzzle Box area. The arrangement of these bones reflects reworking as described in our previous work, and without considering the possibility of reworking by hominins, one mechanism that conceivably might cause reworking was downward movement of sediments into subsurface drains. Further exploration and mapping, combined with additional excavation into the sediments beneath the Puzzle Box area provided more information relevant to this hypothesis. In particular this evidence shows that subsurface drains cannot explain the arrangement of skeletal material observed within the Puzzle Box area. As now discussed in the text, the reworking is selective and initiated from above rather than below. This is best explained by hominin activity subsequent to burial. 

In a new section of the Results we discuss slumping as a hypothesis for the deposition of the remains. This includes discussion of downslope movement within the Hill Antechamber and the idea that floor drains may have been a mechanism for sediment reworking in and around the Puzzle Box area and Dinaledi Feature 1. As described in this section the evidence does not support these hypotheses. 

Hypothesis testing and parsimony

Referees 1 and 3 and the editorial guidance all suggested that a more appropriate presentation would adopt a null hypothesis and test it. The specific suggestion that the null hypothesis should be a natural sedimentary process of deposition was provided not only by these reviewers but also by some outside commentators. To address this comment, we have edited the manuscript in two ways. The first is the addition of a section to the Discussion that specifically discusses hypothesis testing and parsimony as related to Pleistocene evidence of cultural burial. This includes a brief synopsis of recent disciplinary conversations and citation of work by other groups of authors, none of whom adopted this “null hypothesis” approach in their published work. 

As we now describe in the manuscript, previous work on the Dinaledi evidence never assumed any role for H. naledi in the burial of remains. Reading the reviewer reports caused us to realize that this previous work had followed exactly the “null hypothesis” approach that some suggested we follow. By following this null hypothesis approach, we neglected a valuable avenue of investigation. In retrospect, we see how this approach impeded us from understanding the pattern of evidence within the Puzzle Box area. Thus in the revised manuscript we have mentioned this history within the Discussion and also presented more of the background to our previous work in the Introduction. Hopefully by including this discussion of these issues, the manuscript will broaden conversation about the relation of parsimony to these issues. 

Language and presentation style

Reviewer 4 criticizes our presentation, suggesting that the text “gives the impression that a hypothesis was formulated before data were collected.” Other outside commentators have mentioned this notion also, including Martinón-Torres et al. (2024) who suggest that the study began from a preferred hypothesis and gathered data to support it. The accurate communication of results and hypotheses in a scientific article is a broader issue than this one study. Preferences about presentation style vary across fields of study as well as across languages. We do not regret using plain language where possible. In any study that combines data and methods from different

scientific disciplines, the use of plain language is particularly important to avoid misunderstandings where terms may mean different things in different fields. 

The essential question raised by these comments is whether it is appropriate to present the results of a study in terms of the hypothesis that is best supported. As noted above, we read carefully many recent studies of Pleistocene burial evidence. We note that in each of these studies that concluded that burial is the best hypothesis, the authors framed their results in the same way as our previous manuscript: an introduction that briefly reviews background evidence for treatment of the dead, a presentation of results focused on how each analysis supports the hypothesis of burial for the case, and then in some (but not all) cases discussion of why some alternative hypotheses could be rejected. We do not infer from this that these other studies started from a presupposition and collected data only to confirm it. Rather, this is a simple matter of presentation style. 

The alternative to this approach is to present an exhaustive list of possible hypotheses and to describe how the data relate to each of them, at the end selecting the best. This is the approach that we have followed in the revised manuscript, as described above under the direction of the reviewer and editorial guidance. This approach has the advantage of bringing together evidence in different combinations to show how each data point rejects some hypotheses while supporting others. It has the disadvantage of length and repetition. 

Possible artifact

We have chosen to keep the description of the possible artifact associated with the Hill Antechamber Feature in the Supplementary Information. We do this while acknowledging that this is against the opinion of reviewer 4, who felt the description should be removed unless the object in question is fully excavated and physically analyzed. The previous version of the manuscript did not rely upon the stone as positive evidence of grave goods or symbolic content, and it noted that the data do not test whether the possible artifact was placed or was intentionally modified. However this did not satisfy reviewer 4, and some outside commentators likewise asserted that the object must be a “geofact” and that it should be removed. 

We have three arguments against this line of thinking. First, we do not omit data from our reporting. Whether Homo naledi shaped the rock or not, used it as a tool or not, whether the rock was placed with the body or not, it is unquestionably there. Omitting this one object from the report would be simply dishonest. Second, the data on this rock are at 16 micron resolution. While physical inspection of its surface may eventually reveal trace evidence and will enable better characterization of the raw material, no mode of surface scanning will produce better evidence about the object’s shape. Third, the position of this possible artifact within the feature provides significant information about the deposition of the skeletal material and associated sediments. The pitch, orientation, and position of the stone is not consistent with slow deposition but are consistent with the hypothesis that the surrounding sediment was rapidly emplaced at the same time as the articulated elements less than 2 cm away. 

In the current version, we have redoubled our efforts to provide information about the position and shape of this stone while not presupposing the intentionality of its shape or placement. We add here that the attitude expressed by referee 4 and other commentators, if followed at other sites, would certainly lead to the loss or underreporting of evidence, which we are trying to avoid.  

Consistency versus variability of behavior

As described in the revised manuscript, different features within the Dinaledi Subsystem exhibit some shared characteristics. At the same time, they vary in positioning, representation of individuals and extent of commingling. Other localities within the subsystem and broader cave system present different evidence. Some commentators have questioned whether the patterning is consistent with a single common explanation, or whether multiple explanations are necessary. To address this line of questioning, we have added several elements to the manuscript. We created a new section on secondary cultural burial, discussing whether any of the situations may reflect this practice. In the Discussion, we briefly review the ways in which the different features support the involvement of H. naledi without interpreting anything about the intentionality or meaning of the behavior. We further added a section to the Discussion to consider whether variation among the features reflects variation in mortuary practices by H. naledi. One aspect of this section briefly cites variation in the location and treatment of skeletal remains at other sites with evidence of burial. 

Grave goods

Some commentators have argued that grave goods are a necessary criterion for recognizing evidence of ancient burial. We added a section to the Discussion to review evidence of grave goods at other Pleistocene sites where burial is accepted. 

References

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Maloney, T. R., Dilkes-Hall, I. E., Vlok, M., Oktaviana, A. A., Setiawan, P., Priyatno, A. A. D., Ririmasse, M., Geria, I. M., Effendy, M. A. R., Istiawan, B., Atmoko, F. T., Adhityatama, S., Moffat, I., Joannes-Boyau, R., Brumm, A., & Aubert, M. (2022). Surgical amputation of a limb 31,000 years ago in Borneo. Nature, 609(7927), 547–551. https://doi.org/10.1038/s41586-022-05160-8

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Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study from Belato, Knight, and co-workers, the authors investigated the Rec domain of a thermophilic Cas9 from Geobacillus stearothermophilus (GeoCas9). The authors investigated three constructs, two individual subdomains of Rec (Rec1 and Rec2) and the full Rec domain. This domain is involved in binding to the guide RNA of Cas9, as well as the RNA-DNA duplex that is formed upon target binding. The authors performed RNA binding and relaxation experiments using NMR for the wild-type domain as well as two-point mutants. They observed differences in RNA binding activities as well as the flexibility of the domain. The authors also performed experiments on fulllength GeoCas9 to determine whether these biophysical differences affect the RNA binding or cleavage activity. Although the authors observed some changes in the thermal stability of the mutant GeoCas9-gRNA complex, they did not observe substantial differences in the cleavage activities of the mutant GeoCas9 variants.

Overall, this manuscript provides a detailed biophysical analysis of the GeoCas9 Rec domain. The NMR assignments for this construct should prove very useful, and the results may provide the grounds for future engineering of higher fidelity variants of GeoCas9. While the NMR results are generally well presented, it is unclear how the results on the isolated Rec domain related to the overall function of full-length GeoCas9. In addition, some conclusions are overstated and not fully supported by the evidence provided. The following major points should be addressed by the authors.

(1) Many of the results rely on the backbone resonance assignments of the three constructs that were used, and the authors have done an excellent job of assigning the Rec1 and Rec2 constructs. However, it is unclear from the descriptions in the text how the full-length Rec construct was assigned. Were these assignments made based on assignments for the individual domains? The authors state that the spectra of individual domains and RecFL overlay very well, but there appear to be many resonances that have chemical shift differences or are only present in one construct. As it stands, it is unclear how the resonances were assigned for residues whose chemical shifts were perturbed, making it difficult to interpret many of the results.

The Reviewer raises an important oversight. In Lines 491-493, we clarify that we were able to transfer the assignments using spectral overlays of the individual domains with GeoRec (i.e. careful analysis of the data in Figure S3). We also cite two new references where a similar approach was applied to Cas9.

(2) The minimal gRNA that was used for the Rec-gRNA binding experiments is unlikely to be a good mimic for the full-length gRNA, as it lacks any of the secondary structure that is most specifically recognized by the REC lobe and the rest of the Cas9 protein. The majority of this RNA is a "spacer" sequence, but spacers are variable, so this sequence is arbitrary. Thus, the interactions that the authors are observing most likely represent non-specific interactions between the Rec domains and RNA. The authors also map chemical shift perturbations and line broadening on structural models with an RNA-DNA duplex bound, but this is not an accurate model for how the Rec domain binds to a single-stranded RNA (for which there is no structural model). Thus, many of the conclusions regarding the RNA binding interface are overstated.

The Reviewer again raises an important point. We have added a section of text explaining the rationale for truncating the gRNA for binding experiments with NMR (Lines 223-235). We chose the 5’end of the gRNA containing the spacer sequence based on crystal structures of NmeCas9 and SpCas9 that show the Rec lobe interacting with this section of nucleic acid. The newly published GeoCas9 cryo-EM structure bound to gRNA, which overlaid well with the NmeCas9 structure, also suggested that this portion of the gRNA could interact with Rec.

Figures S11 and S12 show our gradual truncation of the gRNA and Rec construct to achieve useful atomic detail. Ultimately, a 39nt gRNA containing a 23 base pair spacer sequence was chosen for this study to retain the NMR signal of the complex and because several structures suggested this 39nt sequence would be long enough to interact with the entire Rec lobe.

To investigate the effect of the spacer sequence, we have now measured binding affinities via MST between GeoRec and a 39nt Tnnt2 gRNA and a 39nt gRNA from PDB: 8UZA, containing a different spacer sequence used in the very recent GeoCas9 cryo-EM structure. The observed trends for each gRNA are consistent across the samples. We also measured WT, K267E, and R332A GeoCas9 affinity for the full-length Tnnt2 and PDB:8UZA gRNAs.

Lastly, we used a new cryo-EM structure of GeoCas9 bound to gRNA (PDB: 8JTR) to better define the interface for NMR CSPs and line broadening and have adjusted the language in this section.

(3) The authors include microscale thermophoresis (MST) data for the Rec constructs binding to the minimal gRNA. These data suggest that all three Rec variants have very similar Kd's for the RNA. Given these similarities, it is unclear why the RNA titration experiments by NMR yielded such different results. Moreover, in the Discussion, the authors state that the NMR titration data are consistent with the MST-derived Kd values. This conclusion appears to be overstated given the very small differences in affinities measured by MST.

MST and NMR experiments describing the weakened binding affinity of GeoRec and GeoRec2 for the Tnnt2 gRNA agree with each other (Figure 5). However, additional MST experiments with a different gRNA sequence (from PDB: 8UZA) and with fulllength GeoCas9 (new Figure 7) have provided new insight for us to soften and reframe the Discussion to avoid overstatement. See Lines 263-282 and 375-385.

(4) While the authors have performed some experiments to help place their findings on the isolated Rec domain in the context of the full-length protein, these experiments do not fully support the conclusions that the authors draw about the meaning of their NMR results. The two Cas9 variants that were explored via NMR have no effect on Cas9 cleavage activity, and it is unclear from the data provided whether they have any effect on GeoCas9 binding to the full sgRNA. This makes it difficult to determine whether the observed differences in RNA binding and dynamics of the isolated Rec domain have any consequence in the context of the full protein.

We have since measured the binding affinities of full-length GeoCas9 to full-length gRNA. (new Figure 7) We have also added a comment in the Discussion section describing how both GeoRec and GeoRec2 domain variants bind the truncated RNA with weaker affinity than the WT, but this biophysical effect does not translate to GeoCas9 with its full-length gRNA. We describe this finding as an explanation for why the single-point mutants have minimal effect of GeoCas9 cleavage activity. See Lines 375-385.

(5) The authors state in multiple places that the K267E/R332A mutant enhanced GeoCas9 specificity. Improved specificity refers to a situation in which the efficiency of cleavage of a perfectly matched target improves in comparison to a mismatched target. This is not what the authors observed for the double mutant. Instead, the cleavage of the perfect target was drastically reduced, in some cases to a larger degree than for the mismatched target. The double mutant does not appear to have improved specificity, it has simply decreased cleavage efficiency of the enzyme.

The conclusion has been reframed to suggest that the K267E/R332A double mutant has decreased cleavage efficiency of the enzyme but does not enhance GeoCas9 specificity. We discuss an interesting contrast, namely that mutations in the SpCas9 Rec lobe alter its specificity, which is at times accompanied by a loss of overall activity. We also speculate on why this may not be the case in GeoCas9, considering some very recent (unpublished at the time of initial submission) structural and biochemical data. See Lines 414-418.

Reviewer #2 (Public Review):

Summary:

The manuscript from Belato et al. used advanced NMR approaches and a mutagenesis campaign to probe the conformational dynamics of the recognition lobe (Rec) of the CRISPR Cas9 enzyme from G. stearothermophilus (GeoCas9). Using truncated and full-length constructs they assess the impacts of two different point mutations have on the redistribution and timescale of these motions and assess gRNA recognition and specificity. Single point mutations in the Rec domain in a Cas9 from a related species had profound impacts on- and off-target DNA editing, therefore the authors reasoned analogous mutations in GeoCas9 would have similar effects. However, despite a redistribution of local motions and changes in global stability, their chosen mutations had little impact on DNA editing in the context of the full-length enzyme. Their studies highlight the species-specific complexity of interdomain communication and allosteric mechanisms used by these multi-domain endonucleases. Despite these negative results, their study is highly rigorous, and their approach will broadly support understanding how the activity and specificity of these enzymes can be engineered to tune activity and limit off-target cleavage by these enzymes.

Strengths:

(1) Atomistic investigation of the conformational dynamics of the GeoCas9 gRNA recognition lobe (GeoRec), probing dynamics on a broad range of timescales from ps to ms using advanced NMR approaches will be broadly interesting to both the structural biology and CRISPR engineering communities.

(2) Highly rigorous biophysical studies that push the boundaries of current techniques, provide insight into local dynamics of the GeoRec domain that serve to propagate allosteric information and potentially regulate enzymatic activity.

(3) The study highlights the complexities of understanding interdomain communication in Cas9 enzymes since analogous mutations in different species have different effects on target recognition and cleavage.

(4) The type of structural and dynamic insights derived from this study design could serve as foundational information to guide a rational design strategy aimed at improving the selectivity and reducing the off-target effects of Cas9 enzymes.

Weaknesses:

(1) Despite the rigor of the experiments, the mutations chosen by the authors do not have a profound effect on the overall substrate affinity or activity of GeoCas9 rendering little mechanistic insight into allosteric communication in this particular Cas9. However, the double mutant K267E/R332A has a more pronounced effect on the cleavage of WT and mismatched (at nucleotides 19 and 20) DNA substrates while minimally affecting the cleavage of mismatched (at nucleotides 5 and 6), suggesting more could be learned about the allosteric mechanism from the detailed characterization of this mutant.

We thank the Reviewer for this comment. While we have included new binding experiments with full-length GeoCas9 and gRNAs (new Figure 7), the addition of new MD simulations (new Figure 6) better address this point. MD examined our single and double mutants, as well as the recently published high-specificity iGeoCas9, and reported the degree of conformational sampling and nucleic acid contacts and binding energies.

The simulations show that our mutations induce some, but not the full extent of the effect of iGeoCas9 (with one mutation in GeoRec and many others in the adjacent WED domain), implying that further engineering of GeoRec to mimic iGeoCas9’s properties can have profound functional outcomes. Future efforts to mutate GeoRec will be leverage this strategy. See Lines 309-342.

(2) Follow-up experiments with other residues that were identified as being highly dynamic might affect substrate recognition and cleavage activity in different ways providing additional insight.

The Reviewer is correct. While beyond this initial scope, new MD simulations (see the response directly above) and NMR resonances distally affect by gRNA (via CSP or relaxation dispersion) will be used identify the primary targets for this analysis.

(3) Details regarding the authors' experimental approach are incomplete such as a description of the model used to fit the CD data, a detailed explanation of the global fitting of the relaxation dispersion data describing how the best-fit model was selected, and the description of the ModelFree fitting of fast timescale dynamics is incomplete.

We thank the Reviewer for pointing out these oversights. We have now included the fitting equation in the CD Methods section.

We included new Figures S8-S10 with the individual relaxation dispersion curves and note in the Methods that global fits were deemed superior based on the Akaike Information Criterion. For WT, the AIC showed the global fit to be ~10-fold better. For K267E, the global model was 4-fold better, and for R332A, the global model was 6-fold better.

We have included a more detailed description of CPMG and Model-free fitting. See Lines 520-526.

Reviewer #3 (Public Review):

The authors explore the role of Rec domains in a thermophilic Cas9 enzyme. They report on the crystal structure of part of the recognition lobe, its dynamics from NMR spin relaxation and relaxation-dispersion data, its interaction mode with guide RNA, and the effect of two single-point mutations hypothesised to enhance specificity. They find that mutations have small effects on Rec domain structure and stability but lead to significant rearrangement of micro- to milli-second dynamics which does not translate into major changes in guide RNA affinity or DNA cleavage specificity, illustrating the inherent tolerance of GeoCas9. The work can be considered as a first step towards understanding motions in GeoCas9 recognition lobe, although no clear hotspots were discovered with potential for future rational design of enhanced Cas9 variants.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data, or analyses

(1) Please update the sentences on lines 100-105 and the Methods to clarify how the RecFL assignments were obtained. If RecFL was assigned based on the assignments for Rec1 and Rec2, please describe in the Methods how the shifted resonances were handled. Please also provide chemical shift perturbation profiles for the truncated constructs versus the full-length Rec construct.

We have now added text (Lines 491-493) and two new references explaining the GeoRec (full-length) assignment.

We appreciate this point. We have now provided a new Figure S9 with analysis of CSPs and line broadening in truncated constructs (GeoRec2 only). See also Lines 263-282. We also show a similar structural response to mutation in full-length GeoRec and GeoRec2 NMR CSPs (Figure 2 and Figure S5).

We have provided the CSPs for each construct, relative to the full-length GeoRec domain, Author response image 1. In most cases, the largest CSPs occur at resonances on the periphery of the spectra, retaining the ability to unambiguously assign it.

Author response image 1.

 

(2) It is unclear whether the differences in Kd's for the Rec-gRNA interactions are statistically significant, given the errors associated with the values. Can the authors further analyze these data to determine statistical significance? If they are not found to be significantly different, the authors should soften all conclusions related to the observed differences.

Statistical significance was calculated for all MST data and Figures 5 and 7 have been updated to reflect this

(3) As mentioned above, it seems likely that the Rec-RNA binding that is observed is non-specific. Have the authors tried MST with another 39 nt RNA? Are there differences in affinities for the Rec constructs?

We have done MST with another 39nt RNA. The affinity for each gRNA (Tnnt2 vs 8UZA) is similar for WT and K267E, and a factor of ~4 weaker for R332A with 8UZA gRNA. The trend is the same, that WT Rec has a (statistically significant) stronger affinity for the gRNA compared to the mutants.

(4) Have the authors tried MST with full-length GeoCas9 and the sgRNA? The current data on the thermal stability of the RNP's is interesting, but a more direct measurement of the affinity of the Cas9-sgRNA complexes would provide stronger evidence of the effects of the mutations.

The Reviewer makes an excellent suggestion. We have now generated Cy5-labeled full-length gRNAs and conducted MST with full-length GeoCas9 (new Figure 7). The binding affinities to multiple guides do not vary significantly. We have discussed this, and its implications, in Lines 376-385.

(5) One potential issue with not observing differences between the three Cas9 variants' cleavage activity is that the activity of these purified proteins appears to be very low in comparison to previous studies of GeoCas9. There are significant differences in the expression protocol used by the authors of the current study and previous studies. Have the authors attempted to replicate the expression and purification protocol of previous reports? This may improve the enzymatic activity and allow for a more detailed investigation of cleavage between the three variants (e.g. by performing time-course cleavage assays).

The expression protocol of GeoCas9 is identical to those of previous studies. This was a written mistake on our part, which has now been corrected in the methods section. We apologize for this oversight.

Recommendations for improving the writing and presentation

The introduction of the manuscript is reasonable for specialists who are very familiar with Cas9 function, but it does not contain important details that may be unknown to most readers. The authors do not introduce the domains of Cas9 in the Introduction section. A brief description of the domains that are important to this work should be provided. For example, what is the role of the Rec lobe? This is not introduced until lines 110-111, after some discussion of the authors' initial work on these domains. For a broad audience, it would also be helpful to define the two catalytic domains of the protein. A paragraph describing the general architecture of Cas9 and the overall mechanism of Cas9, including allostery and domain movement, would be very helpful to a general audience. There are elements of this throughout the manuscript, but it would be better to have everything described in a single location at the beginning of the Introduction.

The Reviewer makes an excellent point. We have added significant clarifying text to the Introduction (Lines 42-47, 52-58, and 61-66). We have also amended Figure 1 to highlight the domain arrangement of GeoCas9 and construct domain boundaries.

Minor corrections to the text

(1) Lines 37-38: The statement about GeoCas9 activity should reference citation.

We have added two references here.

(2) Line 39-40: "The widely-studied SpCas9, as well as GeoCas9, are Type-II CRISPR systems". Cas9 is only a single component of a larger system that contains other proteins and DNA elements, so it would be more appropriate to say "are effectors of type II CRISPR systems" or "are signature proteins of type II CRISPR systems". Also, please define the organism from which SpCas9 is derived. It may be more appropriate to use the three-letter abbreviation "SpyCas9" to be consistent with the abbreviation used for GeoCas9.

We have revised the initial suggestion and specified the organisms. We have, however, chosen to keep “SpCas9” for consistency with our prior work and the work of many several others, including Doudna et al and Zhang et al.

(3) Lines 39-42: "only the Type II-C class to which GeoCas9 belongs has been rigorously validated for mammalian genome editing". SpCas9 is from a type II-A system and is by far the most commonly used ortholog for genome editing, including in ongoing clinical trials. It is unlikely that any of the type II-C Cas9 orthologs have been more rigorously validated than SpCas9. The reference cited in this sentence also does not support this statement and is a review written in 2017, so would be unlikely to reflect the current state of the art. Please revise this sentence.

We have softened and revised this text (Lines 42-47).

(4) Lines 48-52: It would be helpful to describe the dynamic movement of the HNH domain (and cite appropriate references) prior to describing the authors' previous work. As it stands, it is unclear how this sentence would be understood by a non-specialist.

We have added text in Lines 61-68

(5) Lines 44-45: The wording is a little unclear, as it sounds like the guide RNA, rather than the nuclease domains, is responsible for dsDNA cleavage. The sentence could be adjusted to remove "and cleave". Cleavage by the HNH and RuvC domains could be described in a separate sentence.

We have revised this text. See Lines 49-50.

(6) Lines 46-48: This segment of the sentence suggests that PAM recognition triggers the allosteric events that result in the movement of the nuclease domain (HNH). This is misleading, as HNH movement is triggered by the complete formation of an R-loop, rather than initial PAM recognition. Please revise this sentence.

We have revised the text in Lines 52-58.

(7) Lines 62-65: The first sentence is unclear. The specificity of many protein-nucleic acid complexes is well understood and is also readily quantified by several wellestablished methods. Are the authors specifically referring to the structural basis for Cas9 specificity? Although Cas9 specificity is highly complex, it has been studied structurally in great detail and should not be described as "poorly understood" without some discussion of what is already known. These sentences also elide the fact that Cas9 specificity has been successfully altered via rational design, based on our general framework for understanding protein-nucleic acid interactions. Please clarify these statements.

The Reviewer makes an important point. We have softened this statement (Lines 8081). We have clarified that we intended to refer to structural characterization of large, multidomain proteins and nucleic acid complexes via NMR. We agree that many critical structural studies comment on Cas9 dynamics and specificity in great detail, including at the domain-level.

(8) Lines 62-68: It seems like the citations do not match up with the references in this section. The references for citations 8-10 are not about DNA repair complexes, references 11-14 are not papers about the directed evolution of Cas9 (should these be 16-17?), and the references for the HNH domain movements should be for citations 1821.

We apologize for the confusion, and the references have been updated

(9) Lines 116-119: The description of the RNAs used is unclear, as the segments that are described add up to 141 not 101. Also, what is meant by "110-nt guide sequence intrinsic to GeoCas9"? Is this referring to the tracrRNA segment? It may be helpful if the RNA sequences shown in the accompanying figures were replaced with cartoons of the RNAs that were used, with the different segments labeled.

We now describe the gRNA sequences in detail in new Table S4. We also expanded a bit in the text (Lines 224-235).

(10) Line 121-123: This sentence should contain reference(s).

We have changed the sentence.

(11) Line 156-158: Reference 19 did not report or investigate any higher specificity SpCas9 variants, is this citation correct?

We have removed the reference from this line. Ref. 19 (now Ref 23, Slaymaker et al) should be correct.

(12) Lines 162-166: Please provide a sequence and structural alignment for SpCas9 and GeoCas9 to support the claim that the amino acid substitutions are equivalent between the two orthologs.

We have updated Figure 1 to display the similarity in domain arrangement between SpCas9 and GeoCas9 and have noted similarity in structure and sequence of these proteins in Figure S1.

(13) Lines 234-236: There is insufficient evidence to conclude that the alterations in protein dynamics caused the changes in gRNA interaction. The substitutions are charge swap substitutions, and it is equally (if not more) feasible that these substitutions decrease the potential for favorable electrostatic interactions.

(14) Lines 261-265: While the RNP stability for R332A is clearly decreased in comparison to WT, the authors' conclusions regarding K267E seem overstated. The difference in Tm for the K267E mutant and WT RNPs is not very large and may be within error, especially given that the CD data are noisy. Similarly, on lines 321-322, only one of the mutations really impacted the stability of the full-length RNP.

We have softened this text in Lines 303-305.

(15) Lines 336-338: HiFi-SpCas9 does not contain four mutations, it is a single R691A point mutation, as reported in reference 17. This sentence and subsequent sentences should be updated.

Here, the “final form” of HiFi SpCas9 contains the R691A and three additional mutations. The Reviewer is correct, though, that the R691A mutation alone was enough to enhance the specificity of WT SpCas9. We have clarified this point on Line 156.

Minor corrections to the figures

(16) The cryo-EM structures of GeoCas9 have recently been released on the PDB. The authors may now update figures to include the experimentally determined structure, rather than an AlphaFold model and update the text accordingly.

We have made this change.

(17) For Figure S4, please describe what the red dashed lines are in the top three graphs. Are these the Tm values determined for the two individual Rec domains? How do these compare to the inflection points for the two transitions in the full Rec construct (could be determined by plotting the first derivative data)? Please provide information in the Methods on how the temperature-dependent CD spectral data were fit and Tm's were determined.

We have made these changes in the Figure S4 caption and Methods section.

(18) The blue box denoting the unassigned region is missing from Figure 2C-D, although it is mentioned in the figure legend.

We have added the blue box denoting the unassigned linker.

Reviewer #2 (Recommendations For The Authors):

The manuscript is well-written and generally clear and concise. The following recommendations will help improve the readability and include details important for interpreting the results.

(1) In general, the figures are too small and difficult to interpret, it was hard to discern the differences described in the text (e.g. Figure 1A, E, 4A, etc.), the text labels are illegible in several panels (e.g. Figure 4A, S8B, C, etc.), the chosen colors were difficult to interpret in the structures (Figure 4C, S8G, H, etc.), as well as residues with motion (as balls) were difficult to make out due to size and color usage. Similar story for the dispersion curves (Fig 3A), the plots are chaotically crowded, and it is impossible to interpret (or see) the undelaying data.

We apologize for these difficulties. We have now revised the Figures in several ways. First, we greatly simplified Figure 1, such that it now includes only the domain arrangement, structure, and initial NMR details for GeoRec (essentially A-B of the old Figure 1).

Second, we have reformatted Figure 3 to make the structure maps a bit easier to see.

We certainly appreciate the point made by the Reviewer about the dispersion curves. Our intent here is to illustrate the number of curves that can be fit globally, which substantially increase for K267E and R332A GeoRec3, versus WT. As a compromise, we have included the individual dispersion curves in the SI for each variant. We have also thinned the line weights for each fit, and added NMR order parameters to the main figure to round out the discussion of dynamics.

Third, we have compiled the gRNA titration into Figure 4, removing the CD analysis (to SI), MST data (new Fig 5), and unclear structure maps to focus only on the NMR spectra here.

Fourth, we have created a new Figure 5 focusing on MST studies of two gRNAs with GeoRec, which now include bar charts of affinities with appropriate statistics.

Much of the data trimmed from the prior version of the manuscript figures has been moved to Supporting Information. We have also created two new main text Figures (6 & 7) based on MD simulations and MST studies of full-length GeoCas9 and gRNAs to provide additional context for interpreting the results in prior figures.

(2) Line 39 - this sentence is awkward, could you rephrase it?

We have rephrased this sentence.

(3) There is inconsistent labeling, in Figure S2 the full-length construct is referred to as GeoRecFL while in other places in the text and in Figure 1 it is called GeoRec.

We have changed all references to the intact Rec lobe to “GeoRec.”

(4) It would be helpful to include a cartoon of the domain organization of GeoCas9 and indicate the truncation mutants that were studied in this manuscript.

We included the domain organization in Figure 1A and indicated the amino acid boundaries for each construct on the figure and in the Methods section.

(5) There is significant line broadening that occurs during the titration, not all line broadening is due to changes in rotational correlation time, and differential line broadening may reveal interactions of residues that are in the intermediate regime, certainly, uM affinities measured by the authors, would suggest this, therefore, a plot of I/Io might inform on binding sites, and it might be useful to look at differential broadening as a function of titrant added.

The Reviewer makes a very good point. In addition to the data in Figure 4, which show a clear reduction in gRNA-induced line broadening in larger GeoRec constructs, we included new titration data on smaller GeoRec2 domains (Figure S12). Here, we conducted an I/I0 analysis and added some clarifying language about the possible nature of line broadening in these samples. See new Figure S12 and Lines 268-274.

(6) Line 126 "Importantly, many resonances are also minimally impacted." This statement is unclear since from the plots shown in Figure 1D, it seems that many of the residues are impacted by RNA titration, see the point about differential broadening above, this sort of plot may help pick apart residues that broaden due to RNA contacts (rather than changing rotational correlation).

We have removed this statement, in addition to our revisions above regarding the line broadening.

(7) Line 137 - I am not sure that a max chemical shift of 0.15 ppm constitutes "strong chemical shift perturbations"

The Reviewer makes a good point. We have changed “strong” to “significant” which refers to 1 standard deviation above the 10% trimmed mean of the data. See Line 237.

(8) Line 144 - change to "...experimentally determined structure...".

We have added new lines 135-136 to make this point clear. We reinforced that initial predictions were based on the Alphafold2, since an experimental structure was lacking, but we have now discussed the mutations in context of the new structural data.

(9) The section from lines 150 - 166, comparison of the effect of different mutations in different Cas9 seems more appropriate for the discussion section.

We have added additional text on this point in the Discussion section, within several new paragraphs.

(10) In Figure S6, chemical shifts are observed at the distal site away from the mutations, could the authors discuss?

The Reviewer makes an important observation. Indeed, the CSPs caused by K267E and R332A extend beyond the mutation site. These shifts are mostly close in 3D space to the mutation, and consistent in Figures 2 and S5. New titrations of gRNA into isolated GeoRec2 also activate some distal sites, and new MD simulations suggests the mutations disrupt RNA and DNA contacts, where these distal effects may play a role with full-length gRNAs.

We agree it would be worth mutating distal sites undergoing CSPs to examine their impact on function, but two complicating factors are 1) the lack of substantial gRNA affinity differences in experiments with full-length GeoCas9 and 2) the lack of functional changes in the mutants. In this initial study, it appears difficult to assign an effect to these distal sites in GeoCas9 (beyond speculation). We do have a brief discussion of the distal sites (Lines 293-298) and will follow up this work with more comprehensive mutagenesis studies of these sites.

(11) It appears that the authors fitted the Tm data to some model although this is not mentioned in the text, figure captions, or methods. In the caption for Figure 4D the authors refer to "Fitted thermal denaturation profiles...".

We have added the relevant Equation in the Methods and referenced it in Figure S6 and S14 captions.

(12) Details of the ModelFree fitting are needed, how many residues fit with the minimal models, and how many invoked Rex and other terms? How does the statement in line 191 about the elevated S2 values arising from global tumbling compare with an experimental estimation of rotational correlation eg. from R2/R1 ratios?

We have included an expanded description of the Model-free protocol (Lines 521-527). The best diffusion tensor was an ellipsoid model. The number of residues utilizing Rex was 81, though Rex contribution was very small. The mean and errors for the fast motion (S²_f), slow motion (S²_z) and generalized order parameter were 0.97 ± 0.15, 0.84 ± 0.14, and 0.91 ± 0.20, respectively.

R2/R1 ratios for each of the samples (relaxation conducted on GeoRec2 in isolation) corresponded to an estimated tc of 16.3 ns for all data sets. This value is a bit larger than would be expected for a compact globular protein of 25 kDa, though our X-ray structure of GeoRec2 shows a somewhat elongated domain.

(13) Line 221 - referring to two different figures at the end of the sentence is confusing, maybe place the figure references immediately after the referral in the sentence.

We have resolved due to reshuffling of the Figures.

(14) Line 234 - Fig 4E is mentioned before fig 4D, in fact Fig 4D is not mentioned in the text.

We have reordered and edited many of the Figures, this is now resolved.

(15) Line 243 - what is the saturating concentration to which the authors are referring?

We have amended the Results section to more clearly discuss the effect of gRNA on the GeoRec and (now) GeoRec2 domains. We meant 3-fold excess gRNA-to-protein by “saturating” in the prior version. At that point, CSPs held stable and the degree of line broadening at certain sites had completely obscured the resonance from view.

(16) Fig 4E caption - mentions error of 1.34 while the figure is labeled 1.1 for the R332A GeoRec mutant.

This has been resolved due to additional MST trails as well as the editing and reordering of many Figures.

(17) Line 253 - the authors are discussing regions of allosteric hotspots, how do the motions of these predicted hotspots compare with the relaxation dispersion data? There seems to be some overlap.

The Reviewer makes a keen observation. Yes, there is overlap in these data. For example, hotspot residue R269 is bracketed by L268 and L270 with relaxation dispersion. Also, hotspot L279 surrounded by C275, A276, R277, and D281 with dispersion in both variants. Further, D403 and E408 reside in a stretch of ms timescale flexibility comprised of N404, L406, N412, and L413. We have yet to fully understand the functional significance of this overlap, but have added a note in Line 298 to draw the reader’s attention to it.

Reviewer #3 (Recommendations For The Authors):

Although the scope of the manuscript is rather limited due to the minor effects observed for the selected mutations, it is clear that a lot of work was done in spearheading the investigation of dynamic modes in GeoCas9 Rec2. In my view, the data will still be of relevance and interest to the general structural and chemical biology communities.

However, there are a few technical shortcomings that need to be addressed and some statements that are poorly supported by data, necessitating either more experimental proofs or rephrasing of the conclusions.

Major points:

X-ray structure - No PDB ID, structural statistics, or validation report is given for the structure, so it is impossible to judge of the quality. Please provide these. Furthermore, it would be commendable to determine the structure of the point mutant Rec2 domains, this would greatly strengthen the claim that mutations affect only dynamics and do not change structure.

We apologize for this oversight. We absolutely had these data at the time of submission but must have forgotten to upload them. The validation report is now attached.

Regarding the mutant structures, the Reviewer’s point is well taken. In the absence of these structures, we have adjusted the language to include the possibility of structural change. We have also included new MD simulations (new Figure 6 and associated text) that provide comment on possible structural and dynamic changes due to mutation. We note that NMR spectral changes are quite modest, beyond the site of mutation. Further, the new binding data with full-length GeoCas9 (new Figure 7) shows very little change in gRNA affinity with mutations, implying that a profound structural rearrangement does not take place.

Translating isolated Rec2 findings to FL GeoCas9 - This is an important point and I do appreciate that the authors discuss this. I agree that working on FL samples for NMR would not be feasible, but I am not convinced by the statement that "GeoRec2 in isolation represents the structure of the subdomain within full-length GeoCas9 very well". The chemical shift perturbations observed between isolated Rec2 and FL Cas9 are relatively sizable. This should be discussed in further detail. Figure 1B should showcase peaks having the highest perturbations. Are they located at termini or interaction interfaces?

We have provided the combined ¹H-¹⁵N combined CSPs for each construct, relative to the full-length GeoRec domain, Author response image 1. In most cases, the largest CSPs occur at resonances on the periphery of the spectra, retaining the ability to unambiguously assign it. The largest CSPs do appear to exist at the termini.

The Rec1 and Rec2 subdomains are connected by a short, but flexible unstructured linker in full-length GeoRec. Thus, the two subdomains do not form a particularly tight non-covalent interface and behave somewhat independently (see Figure S4, for example).

Regarding the statement of “GeoRec2 in isolation...,” we apologize for this confusion.

We were referring to our solved crystal structure in relation to the AlphaFold model. With the new cryo-EM structure of GeoCas9 having been recently published, our X-ray structure of GeoRec2 is still in excellent agreement, but we have clarified our intent on Line 111.

Dynamics and effect of mutations - K267E is more destabilizing and leads to more spread chemical shift perturbations throughout Rec2 and to faster-correlated dynamics but not in significantly lower affinity or cleavage. How do the authors explain this?

The Reviewer raises an interesting question. Regarding the impact of the K267E mutation, new MD simulations also suggest K267E to be quite disruptive of the GeoCas9 structure and dynamics, modulating contacts with the nucleic acids. However, further MD analysis of the recently published (bona fide high specificity) iGeoCas9 variant shows that K267E only imparts a portion of the effect of iGeoCas9, suggesting that even further modulation of GeoRec would be require for substantial functional impact. In addition, new MST binding studies with full-length variants and gRNAs show K267E does not dramatically alter gRNA binding, suggesting that the lack of functional impact, despite biophysical change, is suppressed by the surrounding GeoCas9 domains. We comment on this in the Discussion.

Moreover, the time regime for the fit of the CPMG curves is surprisingly slow given the profiles, how were the minor state populations? Were the dynamics really correlated? Please provide numbers (also see minor points below). In that regime CEST experiments should work, was that done?

The minor state populations were very low in the analysis, <1%.

To examine the correlated dynamics, we compared the global fits to those of the individual fits for each residue and found them to be better for the global fit, based on the Akaike Information Criterion. For WT, the AIC showed the global fit to be ~10-fold better. For K267E, the global model was 4-fold better, and for R332A, the global model was 6-fold better. We have added language clarifying the use of AIC to the Methods section.

We have done CEST experiments on _Geo_HNH (we did not see overly clear evidence for a minor state), but we did not perform these experiments on GeoRec. However, we strongly agree that a detailed follow-up study focusing on CEST and new GeoRec variants should investigate this further.

Since the binding effects with gRNAs differ in the isolated domain and the full-length protein, we have tried not to over-analyze the impact of the relaxation data in this specific context. These data still provide useful information regarding the impact of point mutants on GeoCas9 domain biophysics, and MD simulations support the enhanced dynamics seen in CPMG and other relaxation data. However, the functional implication is clearly more complicated and requires further study.

Mutations affect gRNA affinity - I am not convinced that affinity itself is significantly affected based on the MST data. This data could be reproduced as technical replicates to reduce the error bars, or another technique with less intrinsic noise (ITC, SPR) could be used to better support this claim. However, a 3-fold difference seen from NMR titrations could indicate a change in binding mode, for instance in koff. It would be interesting to obtain SPR or BLI data quantifying the kinetics of the interactions. Anyhow, this point should be more carefully discussed.

We agree with the Reviewer on this point. We conducted additional replicates of MST trials, as well as new MST with a different gRNA sequence. Our updated analysis, including statistics, provides a better measure for “significance” in these data, which is now reported. We have also added some text discussing a possible change in binding mode, see Lines 256-259.

We also carried out MST on full-length GeoCas9 with full-length gRNAs (the same two RNAs used as truncated constructs). We report these data in new Figure 7 and note there is essentially no difference between the gRNAs or the GeoCas9 variants under these conditions.

Further, MD simulations suggest a change in binding energy associated with the gRNA interaction in the context of full-length GeoCas9. Since experimental studies are not able to parse these differences, collectively, we describe a scenario where the highly stable structure of GeoCas9 resists substantial mutation-induced change seen for analogous perturbations in SpCas9. See Lines 309-342, 414-418, and 448-461.

Minor points:

• Please detail how the error on R1 and R2 rates was calculated.

We have included new text in Lines 514-518.

• Please detail how hetNOE values were calculated (simply Isat/Iref?) and what values were used for Model Free.

Yes, the Reviewer is correct. We have added specifically that we used Isat/Iref on Line 518.

• Please elaborate on the Model Free analysis. What tensor was used for tumbling? What was the correlation time? This is needed to judge the trustworthiness of S2 parameters.

We have included new text on Lines 520-526. The diffusion tensor used was an ellipsoid and the correlation time was 15.4 ns. The correlation time estimated from R2/R1 ratios was 16.3 ns.

• Figure 1: Please indicate where Rec1 and Rec2 are located on panel A and indicate the residue assignments for each peak showcased in panel B.

We have indicated the boundary of Rec1 and Rec2 in the new cartoon of Figure 1A. We have also noted the exact amino acids used for each construct in the Methods. We also added resonance labels to the spectral overlays in Figure 1B. We have done the same

• Line 187: I believe this should refer to Figure S8C rather than Figure 3A.

We have made this change.

• Some fits of the CPMG curves look strange, e.g. R343 in Fig. 3B WT definitely does not contain significant us-ms dynamics and should be excluded from the analysis. Please double-check each profile. Were other models besides CR72 not providing better fits?

The Reviewer has made a very careful observation. Our intent was to highlight these sites on purpose to show differences in CPMG relaxation dispersion between WT and variant samples. This was provided as some evidence for the redistribution of dynamics between samples, as many different sites found to be “rigid” on the ms timescale in WT GeoRec2 were flexible in GeoRec2 variants. We agree, however, that this Figure panel was confusing and have therefore removed it in favor of simple discussion in the text.

• To what degree are the CPMG dynamics correlated, can you provide statistical measures for the global fits?

We compared the global fits to those of the individual fits for each residue and found them to be better for the global fit, based on the Akaike Information Criterion. For WT, the AIC showed the global fit to be ~10-fold better. For K267E, the global model was 4fold better, and for R332A, the global model was 6-fold better.

We have added language clarifying the use of AIC to the Methods section.

• Error measured from replicates and p-values should be reported for DNA cleavage assays.

We thank the Reviewer for pointing out this omission. We have included error bars on these plots.

Author response:

The following is the authors’ response to the original reviews

Reviewer #2 suggested the addition of new data to address the following points:

Reviewer #2: 

(1) Oncogenic GOF - the main data shown for GOF are the survival curve and enhanced metastasis. Often, GOF is exemplified at the cellular level as enhanced migration and invasion, which are standard assays to support the GOF. As such, the authors should perform these assays using either tumor cells derived from the mice or transformed fibroblasts from these mice. This will provide important and confirmatory evidence for GOF for Y217C. 

We thank the referee for this comment. Our previous data indicated accelerated tumor progression and increased metastasis in Trp53^Y217C/Y217C mice, which provided in vivo evidence of an oncogenic gain of function (GOF) for the p53^Y217C mutant. However, we agree that it was important to provide additional evidence of GOF at the cellular level. 

Many cellular assays were previously used to evaluate the GOF of p53 mutants, including those listed by the referee. Importantly, Zhao et al. recently showed that a common property of several p53 mutants proposed to have oncogenic GOF is their capacity to promote chromosomal instability (Zhao et al. (2024) Nat. Commun. 15, 180). For the revision of our manuscript, we compared the frequencies of chromosomal alterations occurring spontaneously in WT, Trp53^Y217C/Y217C and Trp53^-/- mouse embryonic fibroblasts (MEFs). Chromosome breaks, radial chromosomes and DMs were more frequent in Trp53^Y217C/Y217C MEFs than in WT or Trp53^-/- MEFs, providing clear evidence of a GOF promoting chromosomal instability. This new result is presented in Figure 2G and mentioned in the revised abstract. 

Furthermore, as pointed out by referee #1 in a confidential comment, increased NF-kB signaling provides evidence of p53 GOF. Accordingly, Zhao et al. proposed that the capacity of p53^G245D and p53^R273H to promote chromosomal instability ultimately led to activation of a noncanonical NF-kB signaling that would promote tumor cell invasion and metastasis. Consistent with their work, we now report that the GSEA of Trp53^Y217C/Y217C and Trp53^-/- thymocytes revealed an upregulation of non-canonical NF-kB signaling in Trp53^Y217C/Y217C thymic cells (a new result presented in Figure 5F and Supplementary Figure S13).  These new data lead us to mention in the revised discussion that “similar mechanisms might underlie the oncogenic properties of the p53^Y217C, p53^G245D and p53^R273H mutants”.

(2) Novel target gene activation - while a set of novel targets appears to be increased in the Y217C cells compared to the p53 null cells, it is unclear how they are induced. The authors should examine if mutant p53 can bind to their promoters through CHIP assays, and, if these targets are specific to Y217C and not the other hot-spot mutations. This will strengthen the validity of the Y217C's ability to promote GOF. 

We respectfully disagree with the referee when he/she considers that the validity of p53^Y217C’s ability to promote a GOF would be strengthened by showing that p53^Y217C binds to the promoters of genes upregulated in Trp53^Y217C/Y217C cells. In fact, Pal et al. recently performed the experiment proposed by the referee, by integrating RNAseq and ChIPseq data from MCF10A cells expressing p53^Y220C, the human equivalent of p53^Y217C,  and found that 95% of the genes upregulated upon p53^Y220C expression were upregulated indirectly, without p53^Y220C binding to their promoters (Pal et al. (2023) NPJ Breast Cancer 9, 78). Consistent with our data, Pal et al. notably found that the expression of p53^Y220C increased cell migration and invasion, which correlated with an increased expression of S100A8 and S100A9. They found that the promoters of S100A8 and S100A9 were however not bound by p53^Y220C, indicating an indirect mechanism for their upregulated expression. Furthermore, the study by Zhao et al. mentioned above also suggested an indirect mechanism of GOF, because the upregulation of inflammation-related genes by a mutant p53 protein was proposed to result from signaling cascades triggered by chromosomal instability. Our data appear consistent with both studies, because p53^Y217C was undetectable or barely detectable in the chromatin fraction of Trp53^Y217C/Y217C cells, and because Trp53^Y217C/Y217C cells exhibited increased chromosome instability and increased NFB signaling compared to Trp53^-/- cells, which may suggest indirect mechanisms for p53^Y217C GOF. 

Nevertheless, we agree with the referee that it was important to provide stronger evidence of p53^Y217C GOF in the revised manuscript.  In that regard, we were intrigued by the perinatal death of most Trp53^Y217C/Y217C females, which provided evidence of unexpected teratogenic effects of the mutant. We had proposed that these female-specific teratogenic effects likely resulted from pro-inflammatory GOF of p53^Y217C. This hypothesis relied on the RNAseq pro-inflammatory signature in Trp53^Y217C/Y217C thymic cells, and on the fact that the glycoprotein CD44, known to drive inflammation, had been identified as a key gene in open neural tube defects. However, we had not tested this hypothesis experimentally. In the revised version of the manuscript, we tested this hypothesis. We mated Trp53^+/Y217C female mice with Trp53^Y217C/Y217C males, then administered supformin (LCC-12), a potent CD44 inhibitor known to attenuate inflammation in vivo, to pregnant mice by oral gavage. The administration of subformin led to a five-fold increase in the proportion of weaned Trp53^Y217C/Y217C females in the progeny, suggesting that reducing inflammation in utero rescued some of the Trp53^Y217C/Y217C female embryos. This new result is presented in Figure 5G and Supplementary Table S6, and mentioned in the abstract. 

We believe that these new results, as well as the additional GSEA analyses revealing increased NFkB signaling in Trp53^Y217C/Y217C cells, further emphasize the importance of inflammation in the GOF of the p53^Y217C mutant. Accordingly, we slightly modified the title of our article, to include the notion that Trp53^Y217C is an inflammation-prone mouse model. We also end the article by summarizing the effects of p53^Y217C in vivo, in a new Supplementary Table S7 that compares the LOF effects of a p53 KO with the (LOF+GOF) effects of the p53^Y217C mutant. 

(3) Dominant negative effect - the authors' claim of lack of DN effect needs to be strengthened further, as most p53 hot-spot mutations do exhibit DN effect. At the minimum, the authors should perform additional treatment with nutlin and gamma irradiation (or cytotoxic/damaging agents) and examine a set of canonical p53 target genes by qRT-PCR to strengthen their claim. 

Our previous data indicated identical tumor onset and survival in Trp53^+/Y217C and Trp53^+/- mice, leading us to conclude that, at least for spontaneous tumorigenesis, there was no evidence of a Dominant Negative Effect (DNE) in vivo. Here, we followed the referee’s suggestion and evaluated the possibility of a DNE in response to stress, by comparing WT, Trp53^+/Y217C and Trp53^+/- MEFs or thymocytes. We analyzed different types of stress (Nutlin, Doxorubicin, girradiation) and different types of cellular responses (transactivation of classical p53 target genes, cell cycle arrest, apoptosis), and the results lead us to conclude that there is little if any DNE also in response to various stresses. These new data are mentioned in a paragraph evaluating the possibility of DNE or GOF at the cellular level, and presented in a new Supplementary Figure S6.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Paturi et.al. presents a detailed structural and mechanistic study of the DRB7.2:DRB4 complex in plants, focusing on its role in sequestering endogenous inverted-repeat dsRNA precursors and inhibiting Dicer-like protein 3 (DCL3) activity. By truncating the two proteins, they systematically identify the domains involved in direct interaction between DRB7.2 and DRB4 and study the interactions between the two using biophysical techniques (ITC and NMR). They show using NMR that the interacting domains between the two proteins are likely partially unfolded or aggregated in the absence of the binding partner and determining the NMR structure of the individual interacting domains in the presence of the isotopically unlabelled partner using sparse restrain data combined with Rosetta. They also determine the complex structure of the interacting DRB7.2 dsRBD domain and the DRB4 D3 domain using X-ray crystallography.

Strengths:

Overall, the manuscript is well written, provides molecular details at high resolution between the interaction of DRB7.2 and DRB4, and the data in the manuscript strongly supports the proposed model where DRB7.2:DRB4 complex sequesters the DCL3 substrates inhibiting its function of producing epigenetically activated siRNAs.

Weaknesses:

Major comments:

(1) The manuscript, unfortunately, completely lacks functional validation of the determined DRB7.2:DRB4 complex structure, which is required for the rigorous validation of the proposed model. For functional validation of the determined structures, the author should at least present the mutational analysis (impact on complex formation, RNA affinity) of the point mutants derived from the structure of the DRB7.2:DRB4 complex.

We thank the reviewer for pointing out a crucial aspect that is missed out in our manuscript. With the inputs and experiments proposed above, we would certainly like to perform additional mutational analysis to determine the impact on the heterodimeric complex formation and identify the key essential residues involved in the RNA binding.

We expect that we can accomplish this study in the next ~ 4-6 months as we may have to create a combination of mutations for residues involved in the dimerization interface, namely, T131, V132, E134, F136, W156, and V161 on DRB7.2M. Having said that, the disruption of the heterodimer interface would probably lead to DRB7.2M and DRB4D3 returning to their fast-intermediate timescale exchanging native homo-oligomeric state/partially folded state.

For dsRNA binding, six residues (i.e., A85 and K86 (a1), H112 and K114 (b1-b2 loop), and K142 and K144 (a2)) involved in the RNA binding interface and a few other residues based on the mutational data will be considered.

(2) The proposed model shows the DRB7.2M and DRB4D3 as partially folded/aggregated proteins in the absence of the complex, understandably from the presented NMR data of the individual domains. However, in the cellular context, when the RNAs are present, especially DRB7.2M might be properly folded/not aggregated. Could the authors support or negate this by showing the ¹⁵N HSQC spectrum of DRB7.2M in complex with the 13 bp dsRNA?

While we have no direct proof that the DRB7.2M might be folded/not aggregated in the presence of RNAs in the cellular context, the in vitro NMR-based titration studies of alone DRB7.2 (Author response image 1A) with two molar equivalence of 13 bp dsRNA (Author response image 1B and R1C) indicate that there is no change in overall spectral pattern (except for the apparent chemical shift perturbations as expected from fast-intermediate exchange timescale binding of DRB7.2M with 13 bp dsRNA), implying that the dsRNA alone is neither necessary nor sufficient to disrupt the native fast exchange oligomeric states sampled by individual DRB7.2 and DRB7.2M.

Author response image 1.

DRB7.2M binding interaction with 13bp dsRNA (A) 1H-15N TROSY-HSQC of U[15N, 2H] DRB7.2M. (B) 1H-15N TROSY-HSQC of U[15N, 2H] DRB7.2M in the presence of 13 bp dsRNA with 1:2 molar equivalence. (C) An overlay of (A) and (B) indicates no evident changes in the broadening of resonances. (D) The 15N linewidth analysis of unbound (red) and bound (green) forms of U[15N, 2H] DRB7.2M resonances for which the assignment could be traced from the assignments of the DRB7.2M:DRB4D3 complex.

Furthermore, the line-width analysis, shown in Author response image 1D, implies that the ~R₂ rates are roughly identical in the presence of dsRNA, indicating that the native oligomeric state of DRB7.2M remains unperturbed by the presence of dsRNA. Our observation also corroborates with the crystal structure presented in the manuscript, where we have observed that the hetero-dimeric interface lies on the opposite side of the dsRNA binding interface of the DRB7.2M:DRB4D3 complex.

Therefore, the dsRNA substrate does not have any role in the native partially folded/oligomeric state of DRB7.2M.

(3) It remains unclear from the manuscript if DRB7.1 will have a similar or different mechanism of interaction with DRB4. Based on the sequence comparisons of the two proteins, the authors should comment on this in the discussion section.

Pairwise sequence alignment of full-length DRB7.2 and DRB7.1 reveals 50.7% similarity and a 33.2% identity derived from EMBOSS Needle (Author response image 2).

Author response image 2.

ClustalW alignment of full-length DRB7.2 and DRB7.1. The secondary structure elements are derived from the crystal structure of DRB7.2M (PDB ID: 8IGD). Identical residues are marked with red highlights, whereas similar residues are marked with yellow highlights, and the consensus residues (> 50%) are annotated below the sequence alignment.

As expected, for the dsRBD region (corresponding to DRB7.2M), we observe a much higher degree of alignment with a 76.7% similarity with a 54.7% identity (Author response image 3).

Author response image 3.

ClustalW alignment of the dsRBD region of DRB7.2 and DRB7.1. The secondary structure elements are derived from the crystal structure of DRB7.2M (PDB ID: 8IGD). Identical residues are marked with red highlights, whereas similar residues are marked with yellow highlights, and the consensus residues (> 50%) are annotated below the sequence alignment.

Moreover, the residues involved in the heterodimerization interface in DRB7.2M are identical to those in DRB7.1. As a matter of fact, the residues involved in the dimerization interface, namely, T131, V132, E134, F136, W156, and V161 in DRB7.2M are unchanged in DRB7.1, suggesting that DRB7.1M may interact with DRB4D3 using a similar manner as illustrated for DRB7.2M:DRB4D3 in the manuscript.

Future studies will shed more light on the binding preference of DRB4D3 with DRB7.1 versus DRB7.2. One interesting thing to note is that DRB7.2 is exclusively present in the nucleus, whereas DRB7.1 is observed to localize in the nucleus as well as the cytoplasm. Therefore, spatial restriction may be one of the mechanisms that bring exclusivity to the interaction partner despite having a conserved interaction interface.

Minor comments:

(1) There are no errors for the N, dH, and dS values of the ITC measurements in Table 1. Also, it seems that the measurements are done only once. Values derived from at least triplicates should be presented. This would be helpful to increase confidence in the values derived from ITC, especially for the titration between DRB7.2, DRB4C, and DRB4D3, as the N value there is substantially lower than 1, which does not agree with the other data.

We plan to estimate the errors as proposed by the reviewer in the revised manuscript to ensure that the presented data is of high confidence.

Reviewer #2 (Public review):

Summary:

The manuscript by Paturi and colleagues uses an approach that combines structural biology and biochemistry to probe protein-protein and protein-RNA interactions for two protein factors related to the dsRNA pathway in plants.

Strengths:

A key finding in the research is the direct demonstration of the ability of the single dsRBD (double-strand RNA binding domain) of DRB7.2 to interact simultaneously with dsRNA as well as the C-terminal domain of DRB4. The heterodimerization of DRB7.2 and DRB4 is demonstrated to make a high-affinity complex with dsRNA, and it is proposed that this atypical use of the dsRBD domain to bridge the protein and RNA may contribute to the ability to prevent cleavage that would otherwise occur for dsRNA. The primary results for the interactions are generally well-supported by the data, and the conclusions are taken from the available results without excessive speculation.

Weaknesses:

There is a need for some statistical repeats, as well as a suggested movement of many protein characterization findings in the solution state to support data or to better indicate how these properties could play a role in the final proposed mechanism. There is also the need for certain measurement replicates, such as for the ITC data, which are derived from single measurements and lack sufficient estimates of error.

We plan to restructure the manuscript on the lines proposed by the reviewer in the revised version. Moreover, as mentioned in the response to the comments of Reviewer 1, we suggest estimating the errors to ensure that the presented data is of high confidence in the revised version.

Author response:

We thank the reviewers of this manuscript for their thoughtful and detailed feedback, and agree that they bring up valid points. We also thank them for their suggestions on how to improve this study. We intend to revise this manuscript to help address these concerns and in the future will submit a revised version that will hopefully be improved in terms of the clarity of the text and rigor of the experimental findings.

Author response:

Public Reviews:

Reviewer #1 (Public review):

We thank the reviewer for his valuable input and careful assessment, which have significantly improved the clarity and rigor of our manuscript.

Summary:

Mazer & Yovel 2025 dissect the inverse problem of how echolocators in groups manage to navigate their surroundings despite intense jamming using computational simulations.

The authors show that despite the 'noisy' sensory environments that echolocating groups present, agents can still access some amount of echo-related information and use it to navigate their local environment. It is known that echolocating bats have strong small and large-scale spatial memory that plays an important role for individuals. The results from this paper also point to the potential importance of an even lower-level, short-term role of memory in the form of echo 'integration' across multiple calls, despite the unpredictability of echo detection in groups. The paper generates a useful basis to think about the mechanisms in echolocating groups for experimental investigations too.

Strengths:

(1) The paper builds on biologically well-motivated and parametrised 2D acoustics and sensory simulation setup to investigate the various key parameters of interest

(2) The 'null-model' of echolocators not being able to tell apart objects & conspecifics while echolocating still shows agents successfully emerge from groups - even though the probability of emergence drops severely in comparison to cognitively more 'capable' agents. This is nonetheless an important result showing the direction-of-arrival of a sound itself is the 'minimum' set of ingredients needed for echolocators navigating their environment.

(3) The results generate an important basis in unraveling how agents may navigate in sensorially noisy environments with a lot of irrelevant and very few relevant cues.

(4) The 2D simulation framework is simple and computationally tractable enough to perform multiple runs to investigate many variables - while also remaining true to the aim of the investigation.

Weaknesses:

There are a few places in the paper that can be misunderstood or don't provide complete details. Here is a selection:

(1) Line 61: '... studies have focused on movement algorithms while overlooking the sensory challenges involved' : This statement does not match the recent state of the literature. While the previous models may have had the assumption that all neighbours can be detected, there are models that specifically study the role of limited interaction arising from a potential inability to track all neighbours due to occlusion, and the effect of responding to only one/few neighbours at a time e.g. Bode et al. 2011 R. Soc. Interface, Rosenthal et al. 2015 PNAS, Jhawar et al. 2020 Nature Physics.

We appreciate the reviewer's comment and the relevant references. We have revised the manuscript accordingly to clarify the distinction between studies that incorporate limited interactions and those that explicitly analyze sensory constraints and interference. We have refined our statement to acknowledge these contributions while maintaining our focus on sensory challenges beyond limited neighbor detection, such as signal degradation, occlusion effects, and multimodal sensory integration (see lines 61-64):

While collective movement has been extensively studied in various species, including insect swarming, fish schooling, and bird murmuration (Pitcher, Partridge and Wardle, 1976; Partridge, 1982; Strandburg-Peshkin et al., 2013; Pearce et al., 2014; Rosenthal, Twomey, Hartnett, Wu, Couzin, et al., 2015; Bastien and Romanczuk, 2020; Davidson et al., 2021; Aidan, Bleichman and Ayali, 2024), as well as in swarm robotics agents performing tasks such as coordinated navigation and maze-solving (Faria Dias et al., 2021; Youssefi and Rouhani, 2021; Cheraghi, Shahzad and Graffi, 2022), most studies have focused on movement algorithms , often assuming full detection of neighbors (Parrish and Edelstein-Keshet, 1999; Couzin et al., 2002, 2005; Sumpter et al., 2008; Nagy et al., 2010; Bialek et al., 2012; Gautrais et al., 2012; Attanasi et al., 2014). Some models have incorporated limited interaction rules where individuals respond to one or a few neighbors due to sensory constraints (Bode, Franks and Wood, 2011; Jhawar et al., 2020). However, fewer studies explicitly examine how sensory interference, occlusion, and noise shape decision-making in collective systems (Rosenthal et al., 2015).

(2) The word 'interference' is used loosely places (Line 89: '...took all interference signals...', Line 319: 'spatial interference') - this is confusing as it is not clear whether the authors refer to interference in the physics/acoustics sense, or broadly speaking as a synonym for reflections and/or jamming.

To improve clarity, we have revised the manuscript to distinguish between different types of interference:

· Acoustic interference (jamming): Overlapping calls that completely obscure echo detection, preventing bats from perceiving necessary environmental cues.

· Acoustic interference (masking): Partial reduction in signal clarity due to competing calls.

· Spatial interference: Physical obstruction by conspecifics affecting movement and navigation.

We have updated the manuscript to use these terms consistently and explicitly define them in relevant sections (see lines 87-94 and 329-330). This distinction ensures that the reader can differentiate between interference as an acoustic phenomenon and its broader implications in navigation.

(3) The paper discusses original results without reference to how they were obtained or what was done. The lack of detail here must be considered while interpreting the Discussion e.g. Line 302 ('our model suggests...increasing the call-rate..' - no clear mention of how/where call-rate was varied) & Line 323 '..no benefit beyond a certain level..' - also no clear mention of how/where call-level was manipulated in the simulations.

All tested parameters, including call rate dynamics and call intensity variations, are detailed in the Methods section and Tables 1 and 2. Specifically:

· Call Rate Variation: The Inter-Pulse Interval (IPI) was modeled based on documented echolocation behavior, decreasing from 100 msec during the search phase to 35 msec (~28 calls per second) at the end of the approach phase, and to 5 msec (200 calls per second) during the final buzz (see Table 2). This natural variation in call rate was not manually manipulated in the model but emerged from the simulated bat behavior.

· Call Intensity Variation: The tested call intensity levels (100, 110, 120, 130 dB SPL) are presented in Table 1 under the “Call Level” parameter. The effect of increasing call intensity was analyzed in relation to exit probability, jamming probability, and collision rate. This is now explicitly referenced in the Discussion.

We have revised the manuscript to explicitly reference these aspects in the Results and Discussion sections.

Reviewer #2 (Public review):

We are grateful for the reviewer’s insightful feedback, which has helped us clarify key aspects of our research and strengthen our conclusions.

This manuscript describes a detailed model of bats flying together through a fixed geometry. The model considers elements that are faithful to both bat biosonar production and reception and the acoustics governing how sound moves in the air and interacts with obstacles. The model also incorporates behavioral patterns observed in bats, like one-dimensional feature following and temporal integration of cognitive maps. From a simulation study of the model and comparison of the results with the literature, the authors gain insight into how often bats may experience destructive interference of their acoustic signals and those of their peers, and how much such interference may actually negatively affect the groups' ability to navigate effectively. The authors use generalized linear models to test the significance of the effects they observe.

In terms of its strengths, the work relies on a thoughtful and detailed model that faithfully incorporates salient features, such as acoustic elements like the filter for a biological receiver and temporal aggregation as a kind of memory in the system. At the same time, the authors' abstract features are complicating without being expected to give additional insights, as can be seen in the choice of a two-dimensional rather than three-dimensional system. I thought that the level of abstraction in the model was perfect, enough to demonstrate their results without needless details. The results are compelling and interesting, and the authors do a great job discussing them in the context of the biological literature.

The most notable weakness I found in this work was that some aspects of the model were not entirely clear to me.

For example, the directionality of the bat's sonar call in relation to its velocity. Are these the same?

For simplicity, in our model, the head is aligned with the body, therefore the direction of the echolocation beam is the same as the direction of the flight.

Moreover, call directionality (directivity) is not directly influenced by velocity. Instead, directionality is estimated using the piston model, as described in the Methods section. The directionality is based on the emission frequency and is thus primarily linked to the behavioral phases of the bat, with frequency shifts occurring as the bat transitions from search to approach to buzz phases. During the approach phase, the bat emits calls with higher frequencies, resulting in increased directionality. This is supported by the literature (Jakobsen and Surlykke, 2010; Jakobsen, Brinkløv and Surlykke, 2013). This phase is also associated with a natural reduction in flight speed, which is a well-documented behavioral adaptation in echolocating bats (Jakobsen et al., 2024).

To clarify this in the manuscript, we have updated the text to explicitly state that directionality follows phase-dependent frequency changes rather than being a direct function of velocity, see lines 460-465.

If so, what is the difference between phi_target and phi_tx in the model equations?

represents the angle between the bat and the reflected object (target).

the angle [rad], between the masking bat and target (from the transmitter’s perspective)

refers to the angle between the transmitting conspecific and the receiving focal bat, from the transmitter’s point of view.

represents the angle between the receiving bat and the transmitting bat, from the receiver’s point of view.

These definitions have been explicitly stated in the revised manuscript to prevent any ambiguity (lines 467-468). Additionally, a Supplementary figure demonstrating the geometrical relations has been added to the manuscript.

Author response image 1.

What is a bat's response to colliding with a conspecific (rather than a wall)?

In nature, minor collisions between bats are common and typically do not result in significant disruptions to flight (Boerma et al., 2019; Roy et al., 2019; Goldstein et al., 2024).Given this, our model does not explicitly simulate the physical impact of a collision event. Instead, during the collision event the bat keeps decreasing its velocity and changing its flight direction until the distance between bats is above the threshold (0.4 m). We assume that the primary cost of such interactions arises from the effort required to avoid collisions, rather than from the collision itself. This assumption aligns with observations of bat behavior in dense flight environments, where individuals prioritize collision avoidance rather than modeling post-collision dynamics.

From the statistical side, it was not clear if replicate simulations were performed. If they were, which I believe is the right way due to stochasticity in the model, how many replicates were used, and are the standard errors referred to throughout the paper between individuals in the same simulation or between independent simulations, or both?

The number of repetitions for each scenario is detailed in Table 1, but we included it in a more prominent location in the text for clarity. Specifically, we now state (Lines 274-275):

"The number of repetitions for each scenario was as follows: 1 bat: 240; 2 bats: 120; 5 bats: 48; 10 bats: 24; 20 bats: 12; 40 bats: 12; 100 bats: 6."

Regarding the reported standard errors, they are calculated across all individuals within each scenario, without distinguishing between different simulation trials.

We clarified in the revised text (Lines 534-535 in Statistical Analysis)

Overall, I found these weaknesses to be superficial and easily remedied by the authors. The authors presented well-reasoned arguments that were supported by their results, and which were used to demonstrate how call interference impacts the collective's roost exit as measured by several variables. As the authors highlight, I think this work is valuable to individuals interested in bat biology and behavior, as well as to applications in engineered multi-agent systems like robotic swarms.

Reviewer #3 (Public review):

We sincerely appreciate the reviewer’s thoughtful comments and the time invested in evaluating our work, which have greatly contributed to refining our study.

We would like to note that in general, our model often simplifies some of the bats’ abilities, under the assumption that if the simulated bats manage to perform this difficult task with simpler mechanisms, real better adapted bats will probably perform even better. This thought strategy will be repeated in several of the answers below.

Summary:

The authors describe a model to mimic bat echolocation behavior and flight under high-density conditions and conclude that the problem of acoustic jamming is less severe than previously thought, conflating the success of their simulations (as described in the manuscript) with hard evidence for what real bats are actually doing. The authors base their model on two species of bats that fly at "high densities" (defined by the authors as colony sizes from tens to tens of thousands of individuals and densities of up to 33.3 bats/m2), Pipistrellus kuhli and Rhinopoma microphyllum. This work fits into the broader discussion of bat sensorimotor strategies during collective flight, and simulations are important to try to understand bat behavior, especially given a lack of empirical data. However, I have major concerns about the assumptions of the parameters used for the simulation, which significantly impact both the results of the simulation and the conclusions that can be made from the data. These details are elaborated upon below, along with key recommendations the authors should consider to guide the refinement of the model.

Strengths:

This paper carries out a simulation of bat behavior in dense swarms as a way to explain how jamming does not pose a problem in dense groups. Simulations are important when we lack empirical data. The simulation aims to model two different species with different echolocation signals, which is very important when trying to model echolocation behavior. The analyses are fairly systematic in testing all ranges of parameters used and discussing the differential results.

Weaknesses:

The justification for how the different foraging phase call types were chosen for different object detection distances in the simulation is unclear. Do these distances match those recorded from empirical studies, and if so, are they identical for both species used in the simulation?

The distances at which bats transition between echolocation phases are identical for both species in our model (see Table 2). These distances are based on well-documented empirical studies of bat hunting and obstacle avoidance behavior (Griffin, Webster and Michael, 1958; Simmons and Kick, 1983; Schnitzler et al., 1987; Kalko, 1995; Hiryu et al., 2008; Vanderelst and Peremans, 2018). These references provide extensive evidence that insectivorous bats systematically adjust their echolocation calls in response to object proximity, following the characteristic phases of search, approach, and buzz.

To improve clarity, we have updated the text to explicitly state that the phase transition distances are empirically grounded and apply equally to both modeled species (lines 430-447).

What reasoning do the authors have for a bat using the same call characteristics to detect a cave wall as they would for detecting a small insect?

In echolocating bats, call parameters are primarily shaped by the target distance and echo strength. Accordingly, there is little difference in call structure between prey capture and obstacles-related maneuvers, aside from intensity adjustments based on target strength (Hagino et al., 2007; Hiryu et al., 2008; Surlykke, Ghose and Moss, 2009; Kothari et al., 2014). In our study, due to the dense cave environment, the bats are found to operate in the approach phase nearly all the time, which is consistent with natural cave emergence, where they are navigating through a cluttered environment rather than engaging in open-space search. For one of the species (Rhinopoma M.), we also have empirical recordings of individuals flying under similar conditions (Goldstein et al., 2024). Our model was designed to remain as simple as possible while relying on conservative assumptions that may underestimate bat performance. If, in reality, bats fine-tune their echolocation calls even earlier or more precisely during navigation than assumed, our model would still conservatively reflect their actual capabilities.

We actually used logarithmically frequency modulated (FM) chirps, generated using the MATLAB built-in function chirp(t, f0, t1, f1, 'logarithmic'). This method aligns with the nonlinear FM characteristics of Pipistrellus kuhlii (PK) and Rhinopoma microphyllum (RM) and provides a realistic approximation of their echolocation signals. We acknowledge that this was not sufficiently emphasized in the original text, and we have now explicitly highlighted this in the revised version to ensure clarity (sell Lines 447-449 in Methods).

The two species modeled have different calls. In particular, the bandwidth varies by a factor of 10, meaning the species' sonars will have different spatial resolutions. Range resolution is about 10x better for PK compared to RM, but the authors appear to use the same thresholds for "correct detection" for both, which doesn't seem appropriate.

The detection process in our model is based on Saillant’s method using a filter bank, as detailed in the paper (Saillant et al., 1993; Neretti et al., 2003; Sanderson et al., 2003). This approach inherently incorporates the advantages of a wider bandwidth, meaning that the differences in range resolution between the species are already accounted for within the signal-processing framework. Thus, there is no need to explicitly adjust the model parameters for bandwidth variations, as these effects emerge from the applied method.

Also, the authors did not mention incorporating/correcting for/exploiting Doppler, which leads me to assume they did not model it.

The reviewer is correct. To maintain model simplicity, we did not incorporate the Doppler effect or its impact on echolocation. The exclusion of Doppler effects was based on the assumption that while Doppler shifts can influence frequency perception, their impact on jamming and overall navigation performance is minor within the modelled context.

The maximal Doppler shifts expected for the bats in this scenario are of ~ 1kHz. These shifts would be applied variably across signals due to the semi-random relative velocities between bats, leading to a mixed effect on frequency changes. This variability would likely result in an overall reduction in jamming rather than exacerbating it, aligning with our previous statement that our model may overestimate the severity of acoustic interference. Such Doppler shifts would result in errors of 2-4 cm in localization (i.e., 200-400 micro-seconds) (Boonman, Parsons and Jones, 2003). 

We have now explicitly highlighted this in the revised version (see Lines 468-470).

The success of the simulation may very well be due to variation in the calls of the bats, which ironically enough demonstrates the importance of a jamming avoidance response in dense flight. This explains why the performance of the simulation falls when bats are not able to distinguish their own echoes from other signals. For example, in Figure C2, there are calls that are labeled as conspecific calls and have markedly shorter durations and wider bandwidths than others. These three phases for call types used by the authors may be responsible for some (or most) of the performance of the model since the correlation between different call types is unlikely to exceed the detection threshold. But it turns out this variation in and of itself is what a jamming avoidance response may consist of. So, in essence, the authors are incorporating a jamming avoidance response into their simulation.

We fully agree that the natural variations in call design between the phases contribute significantly to interference reduction (see our discussion in a previous paper in Mazar & Yovel, 2020). However, we emphasize that this cannot be classified as a Jamming Avoidance Response (JAR). In our model, bats respond only to the physical presence of objects and not to the acoustic environment or interference itself. There is no active or adaptive adjustment of call design to minimize jamming beyond the natural phase-dependent variations in call structure. Therefore, while variation in call types does inherently reduce interference, this effect emerges passively from the modeled behavior rather than as an intentional strategy to avoid jamming.

The authors claim that integration over multiple pings (though I was not able to determine the specifics of this integration algorithm) reduces the masking problem. Indeed, it should: if you have two chances at detection, you've effectively increased your SNR by 3dB.

The reviewer is correct. Indeed, integration over multiple calls improves signal-to-noise ratio (SNR), effectively increasing it by approximately 3 dB per doubling of observations. The specifics of the integration algorithm are detailed in the Methods section, where we describe how sensory information is aggregated across multiple time steps to enhance detection reliability.

They also claim - although it is almost an afterthought - that integration dramatically reduces the degradation caused by false echoes. This also makes sense: from one ping to the next, the bat's own echo delays will correlate extremely well with the bat's flight path. Echo delays due to conspecifics will jump around kind of randomly. However, the main concern is regarding the time interval and number of pings of the integration, especially in the context of the bat's flight speed. The authors say that a 1s integration interval (5-10 pings) dramatically reduces jamming probability and echo confusion. This number of pings isn't very high, and it occurs over a time interval during which the bat has moved 5-10m. This distance is large compared to the 0.4m distance-to-obstacle that triggers an evasive maneuver from the bat, so integration should produce a latency in navigation that significantly hinders the ability to avoid obstacles. Can the authors provide statistics that describe this latency, and discussion about why it doesn't seem to be a problem?

As described in the Methods section, the bat’s collision avoidance response does not solely rely on the integration process. Instead, the model incorporates real-time echoes from the last calls, which are used independently of the integration process for immediate obstacle avoidance maneuvers. This ensures that bats can react to nearby obstacles without being hindered by the integration latency. The slower integration on the other hand is used for clustering, outlier removal and estimation wall directions to support the pathfinding process, as illustrated in Supplementary Figure 1.

Additionally, our model assumes that bats store the physical positions of echoes in an allocentric coordinate system (x-y). The integration occurs after transforming these detections from a local relative reference frame to a global spatial representation. This allows for stable environmental mapping while maintaining responsiveness to immediate changes in the bat’s surroundings.

See lines 518-523 in the revied version.

The authors are using a 2D simulation, but this very much simplifies the challenge of a 3D navigation task, and there is an explanation as to why this is appropriate. Bat densities and bat behavior are discussed per unit area when realistically it should be per unit volume. In fact, the authors reference studies to justify the densities used in the simulation, but these studies were done in a 3D world. If the authors have justification for why it is realistic to model a 3D world in a 2D simulation, I encourage them to provide references justifying this approach.

We acknowledge that this is a simplification; however, from an echolocation perspective, a 2D framework represents a worst-case scenario in terms of bat densities and maneuverability:

· Higher Effective Density: A 2D model forces all bats into a single plane rather than distributing them through a 3D volume, increasing the likelihood of overlap in calls and echoes and making jamming more severe. As described in the text: the average distance to the nearest bat in our simulation is 0.27m (with 100 bats), whereas reported distances in very dense colonies are 0.5m, as observed in Myotis grisescens and Tadarida brasiliensis (Fujioka et al., 2021; Sabol and Hudson, 1995; Betke et al., 2008; Gillam et al, 2010)

· Reduced Maneuverability: In 3D space, bats can use vertical movement to avoid obstacles and conspecifics. A 2D constraint eliminates this degree of freedom, increasing collision risk and limiting escape options.

Thus, our 2D model provides a conservative difficult test case, ensuring that our findings are valid under conditions where jamming and collision risks are maximized. Additionally, the 2D framework is computationally efficient, allowing us to perform multiple simulation runs to explore a broad parameter space and systematically test the impact of different variables.

To address the reviewer’s concern, we have clarified this justification in the revised text and will provide supporting references where applicable: (see Methods lines 407-412)

The focus on "masking" (which appears to be just in-band noise), especially relative to the problem of misassigned echoes, is concerning. If the bat calls are all the same waveform (downsweep linear FM of some duration, I assume - it's not clear from the text), false echoes would be a major problem. Masking, as the authors define it, just reduces SNR. This reduction is something like sqrt(N), where N is the number of conspecifics whose echoes are audible to the bat, so this allows the detection threshold to be set lower, increasing the probability that a bat's echo will exceed a detection threshold. False echoes present a very different problem. They do not reduce SNR per se, but rather they cause spurious threshold excursions (N of them!) that the bat cannot help but interpret as obstacle detection. I would argue that in dense groups the mis-assignment problem is much more important than the SNR problem.

There is substantial literature supporting the assumption that bats can recognize their own echoes and distinguish them from conspecific signals (Schnitzler and Bioscience, 2001‏; Kazial, Burnett and Masters, 2001; Burnett and Masters, 2002; Kazial, Kenny and Burnett, 2008; Chili, Xian and Moss, 2009; Yovel et al., 2009; Beetz and Hechavarría, 2022). However, we acknowledge that false echoes may present a major challenge in dense groups. To address this, we explicitly tested the impact of the self-echo identification assumption in our study see Results Figure 4: The impact of confusion on performance, and lines 345-355 in the Discussion.

Furthermore, we examined a full confusion scenario, where all reflected echoes from conspecifics were misinterpreted as obstacle reflections (i.e., 100% confusion). Our results show that this significantly degrades navigation performance, supporting the argument that echo misassignment is a critical issue. However, we also explored a simple mitigation strategy based on temporal integration with outlier rejection, which provided some improvement in performance. This suggests that real bats may possess additional mechanisms to enhance self-echo identification and reduce false detections. See lines XX in the manuscript for further discussion.

The criteria set for flight behavior (lines 393-406) are not justified with any empirical evidence of the flight behavior of wild bats in collective flight. How did the authors determine the avoidance distances? Also, what is the justification for the time limit of 15 seconds to emerge from the opening? Instead of an exit probability, why not instead use a time criterion, similar to "How long does it take X% of bats to exit?"

While we acknowledge that wild bats may employ more complex behaviors for collision avoidance, we chose to implement a simplified decision-making rule in our model to maintain computational tractability.

The avoidance distances (1.5 m from walls and 0.4 m from other bats) were selected as internal parameters to ensure coherent flight trajectories while maintaining a reasonable collision rate. These distances provide a balance between maneuverability and stability, preventing erratic flight patterns while still enabling effective obstacle avoidance. In the revised paper, we have added supplementary figures illustrating the effect of model parameters on performance, specifically focusing on the avoidance distance.

The 15-second exit limit was determined as described in the text (Lines 403-404): “A 15-second window was chosen because it is approximately twice the average exit time for 40 bats and allows for a second corrective maneuver if needed.” In other words, it allowed each bat to circle the ‘cave’ twice to exit even in the most crowded environment. This threshold was set to keep simulation time reasonable while allowing sufficient time for most bats to exit successfully.

We acknowledge that the alternative approach suggested by the reviewer—measuring the time taken for a certain percentage of bats to exit—is also valid. However, in our model, some outlier bats fail to exit and continue flying for many minutes, Such simulations would lead to excessive simulation times making it difficult to generate repetitions and not teaching us much – they usually resulted from the bat slightly missing the opening (see video S1. Our chosen approach ensures practical runtime constraints while still capturing relevant performance metrics.

What is the empirical justification for the 1-10 calls used for integration?

The "average exit time for 40 bats" is also confusing and not well explained. Was this determined empirically? From the simulation? If the latter, what are the conditions? Does it include masking, no masking, or which species?

Previous studies have demonstrated that bats integrate acoustic information received sequentially over several echolocation calls (2-15), effectively constructing an auditory scene in complex environments (Ulanovsky and Moss, 2008; Chili, Xian and Moss, 2009; Moss and Surlykke, 2010; Yovel and Ulanovsky, 2017; Salles, Diebold and Moss, 2020). Additionally, bats are known to produce echolocation sound groups when spatiotemporal localization demands are high (Kothari et al., 2014). Studies have documented call sequences ranging from 2 to 15 grouped calls (Moss et al., 2010), and it has been hypothesized that grouping facilitates echo segregation.

We did not use a single integration window - we tested integration sizes between 1 and 10 calls and presented the results in Figure 3A. This range was chosen based on prior empirical findings and to explore how different levels of temporal aggregation impact navigation performance. Indeed, the results showed that the performance levels between 5-10 calls integration window (Figure 3A)

Regarding the average exit time for 40 bats, this value was determined from our simulations, where it represents the mean time for successful exits under standard conditions with masking.

We have revised the text to clarify these details see, lines 466.

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, the authors explored how galanin affects whole-brain activity in larval zebrafish using wide-field Ca2+ imaging, genetic modifications, and drugs that increase brain activity. The authors conclude that galanin has a sedative effect on the brain under normal conditions and during seizures, mainly through the galanin receptor 1a (galr1a). However, acute "stressors(?)" like pentylenetetrazole (PTZ) reduce galanin's effects, leading to increased brain activity and more seizures. The authors claim that galanin can reduce seizure severity while increasing seizure occurrence, speculated to occur through different receptor subtypes. This study confirms galanin's complex role in brain activity, supporting its potential impact on epilepsy.

Strengths:

The overall strength of the study lies primarily in its methodological approach using whole-brain Calcium imaging facilitated by the transparency of zebrafish larvae. Additionally, the use of transgenic zebrafish models is an advantage, as it enables genetic manipulations to investigate specific aspects of galanin signaling. This combination of advanced imaging and genetic tools allows for addressing galanin's role in regulating brain activity.

Weaknesses:

The weaknesses of the study also stem from the methodological approach, particularly the use of whole-brain Calcium imaging as a measure of brain activity. While epilepsy and seizures involve network interactions, they typically do not originate across the entire brain simultaneously. Seizures often begin in specific regions or even within specific populations of neurons within those regions. Therefore, a whole-brain approach, especially with Calcium imaging with inherited limitations, may not fully capture the localized nature of seizure initiation and propagation, potentially limiting the understanding of Galanin's role in epilepsy.

Furthermore, Galanin's effects may vary across different brain areas, likely influenced by the predominant receptor types expressed in those regions. Additionally, the use of PTZ as a "stressor" is questionable since PTZ induces seizures rather than conventional stress. Referring to seizures induced by PTZ as "stress" might be a misinterpretation intended to fit the proposed model of stress regulation by receptors other than Galanin receptor 1 (GalR1).

The description of the EAAT2 mutants is missing crucial details. EAAT2 plays a significant role in the uptake of glutamate from the synaptic cleft, thereby regulating excitatory neurotransmission and preventing excitotoxicity. Authors suggest that in EAAT2 knockout (KO) mice galanin expression is upregulated 15-fold compared to wild-type (WT) mice, which could be interpreted as galanin playing a role in the hypoactivity observed in these animals.

Indeed, our observation of the unexpected hypoactivity in EAAT2a mutants, described in our description of this mutant (Hotz et al., 2022), prompted us to initiate this study formulating the hypothesis that the observed upregulation of galanin is a neuroprotective response to epilepsy.

However, the study does not explore the misregulation of other genes that could be contributing to the observed phenotype. For instance, if AMPA receptors are significantly downregulated, or if there are alterations in other genes critical for brain activity, these changes could be more important than the upregulation of galanin. The lack of wider gene expression analysis leaves open the possibility that the observed hypoactivity could be due to factors other than, or in addition to, galanin upregulation.

We have performed a transcriptome analysis that we are still evaluation. We can already state that AMPA receptor genes are not significantly altered in the mutant.

Moreover, the observation that in double KO mice for both EAAT2 and galanin, there was little difference in seizure susceptibility compared to EAAT2 KO mice alone further supports the idea that galanin upregulation might not be the reason for the observed phenotype. This indicates that other regulatory mechanisms or gene expressions might be playing a more pivotal role in the manifestation of hypoactivity in EAAT2 mutants.

We agree that upregulation of galanin transcripts is at best one of a suite of regulatory mechanisms that lead to hypoactivity in EAAT2 zebrafish mutants.

These methodological shortcomings and conceptual inconsistencies undermine the perceived strengths of the study, and hinders understanding of Galanin's role in epilepsy and stress regulation.

Reviewer #2 (Public Review):

Summary:

This study is an investigation of galanin and galanin receptor signaling on whole-brain activity in the context of recurrent seizure activity or under homeostatic basal conditions. The authors primarily use calcium imaging to observe whole-brain neuronal activity accompanied by galanin qPCR to determine how manipulations of galanin or the galr1a receptor affect the activity of the whole-brain under non-ictal or seizure event conditions. The authors' Eaat2a-/- model (introduced in their Glia 2022 paper, PMID 34716961) that shows recurrent seizure activity alongside suppression of neuronal activity and locomotion in the time periods lacking seizures is used in this paper in comparison to the well-known pentylenetetrazole (PTZ) pharmacological model of epilepsy in zebrafish. Given the literature cited in their Introduction, the authors reasonably hypothesize that galanin will exert a net inhibitory effect on brain activity in models of epilepsy and at homeostatic baseline, but were surprised to find that this hypothesis was only moderately supported in their Eaat2a-/- model. In contrast, under PTZ challenge, fish with galanin overexpression showed increased seizure number and reduced duration while fish with galanin KO showed reduced seizure number and increased duration. These results would have been greatly enriched by the inclusion of behavioral analyses of seizure activity and locomotion (similar to the authors' 2022 Glia paper and/or PMIDs 15730879, 24002024). In addition, the authors have not accounted for sex as a biological variable, though they did note that sex sorting zebrafish larvae precludes sex selection at the younger ages used. It would be helpful to include smaller experiments taken from pilot experiments in older, sex-balanced groups of the relevant zebrafish to increase confidence in the findings' robustness across sexes. A possible major caveat is that all of the various genetic manipulations are non-conditional as performed, meaning that developmental impacts of galanin overexpression or galanin or galr1a knockout on the observed results have not been controlled for and may have had a confounding influence on the authors' findings. Overall, this study is important and solid (yet limited), and carries clear value for understanding the multifaceted functions that neuronal galanin can have under homeostatic and disease conditions.

Strengths:

- The authors convincingly show that galanin is upregulated across multiple contexts that feature seizure activity or hyperexcitability in zebrafish, and appears to reduce neuronal activity overall, with key identified exceptions (PTZ model).

- The authors use both genetic and pharmacological models to answer their question, and through this diverse approach, find serendipitous results that suggest novel underexplored functions of galanin and its receptors in basal and disease conditions. Their question is well-informed by the cited literature, though the authors should cite and consider their findings in the context of Mazarati et al., 1998 (PMID:982276). The authors' Discussion places their findings in context, allowing for multiple interpretations and suggesting some convincing explanations.

- Sample sizes are robust and the methods used are well-characterized, with a few exceptions (as the paper is currently written).

- Use of a glutamatergic signaling-based genetic model of epilepsy (Eaat2a-/-) is likely the most appropriate selection to test how galanin signaling can alter seizure activity, as galanin is known to reduce glutamatergic release as an inhibitory mechanism in rodent hippocampal neurons via GalR1a (alongside GIRK activation effects). Given that PTZ instead acts through GABAergic signaling pathways, it is reasonable and useful to note that their glutamate-based genetic model showed different effects than did their GABAergic-based model of seizure activity.

Weaknesses:

- The authors do not include behavioral assessments of seizure or locomotor activity that would be expected in this paper given their characterizations of their Eaat2a-/- model in the Glia 2022 paper that showed these behavioral data for this zebrafish model. These data would inform the reader of the behavioral phenotypes to expect under the various conditions and would likely further support the authors' findings if obtained and reported.<br />

We agree that a thorough behavioral assessment would have strengthened the study, but we deemed it outside of the scope of this study.

- No assessment of sex as a biological variable is included, though it is understood that these specific studied ages of the larvae may preclude sex sorting for experimental balancing as stated by the authors.

The study was done on larval zebrafish (5 days post fertilization). The first signs of sexual differentiation become apparent at about 17 days post fertilization (reviewed in Ye and Chen, 2020). Hence sex is no biological variable at the stage studied. 

- The reported results may have been influenced by the loss or overexpression of galanin or loss of galr1a during developmental stages. The authors did attempt to use the hsp70l system to overexpress galanin, but noted that the heat shock induction step led to reduced brain activity on its own (Supplementary Figure 1). Their hsp70l:gal model shows galanin overexpression anyways (8x fold) regardless of heat induction, so this model is still useful as a way to overexpress galanin, but it should be noted that this galanin overexpression is not restricted to post-developmental timepoints and is present during development.

The developmental perspective is an important point to consider. Due to the rapid development of the zebrafish it is not trivial to untangle this. In the zebrafish we first observe epileptic seizures as early as 3 days post fertilization (dpf), where the brain is clearly not well developed yet (e.g. behaviroal response to light are still minimal). Even the 5 dpf stage, where most of our experiments have been conducted, cannot by far not be considered post-development.  

Reviewer #3 (Public Review):

Summary:

The neuropeptide galanin is primarily expressed in the hypothalamus and has been shown to play critical roles in homeostatic functions such as arousal, sleep, stress, and brain disorders such as epilepsy. Previous work in rodents using galanin analogs and receptor-specific knockout has provided convincing evidence for the anti-convulsant effects of galanin.

In the present study, the authors sought to determine the relationship between galanin expression and whole-brain activity. The authors took advantage of the transparent nature of larval zebrafish to perform whole-brain neural activity measurements via widefield calcium imaging. Two models of seizures were used (eaat2a-/- and pentylenetetrazol; PTZ). In the eaat2a-/- model, spontaneous seizures occur and the authors found that galanin transcript levels were significantly increased and associated with a reduced frequency of calcium events. Similarly, two hours after PTZ galanin transcript levels roughly doubled and the frequency and amplitude of calcium events were reduced. The authors also used a heat shock protein line (hsp70I:gal) where galanin transcript levels are induced by activation of heat shock protein, but this line also shows higher basal transcript levels of galanin. Again, the higher level of galanin in hsp70I:gal larval zebrafish resulted in a reduction of calcium events and a reduction in the amplitude of events. In contrast, galanin knockout (gal-/-) increased calcium activity, indicated by an increased number of calcium events, but a reduction in amplitude and duration. Knockout of the galanin receptor subtype galr1a via crispants also increased the frequency of calcium events.

In subsequent experiments in eaat2a-/- mutants were crossed with hsp70I:gal or gal-/- to increase or decrease galanin expression, respectively. These experiments showed modest effects, with eaat2a-/- x gal-/- knockouts showing an increased normalized area under the curve and seizure amplitude.

Lastly, the authors attempted to study the relationship between galanin and brain activity during a PTZ challenge. The hsp70I:gal larva showed an increased number of seizures and reduced seizure duration during PTZ. In contrast, gal-/- mutants showed an increased normalized area under the curve and a stark reduction in the number of detected seizures, a reduction in seizure amplitude, but an increase in seizure duration. The authors then ruled out the role of Galr1a in modulating this effect during PTZ, since the number of seizures was unaffected, whereas the amplitude and duration of seizures were increased.

Strengths:

(1) The gain- and loss-of function galanin manipulations provided convincing evidence that galanin influences brain activity (via calcium imaging) during interictal and/or seizure-free periods. In particular, the relationship between galanin transcript levels and brain activity in Figures 1 & 2 was convincing.

(2) The authors use two models of epilepsy (eaat2a-/- and PTZ).

(3) Focus on the galanin receptor subtype galr1a provided good evidence for the important role of this receptor in controlling brain activity during interictal and/or seizure-free periods.

Weaknesses:

(1) Although the relationship between galanin and brain activity during interictal or seizure-free periods was clear, the manuscript currently lacks mechanistic insight in the role of galanin during seizure-like activity induced by PTZ.

We completely agree and concede that this study constitutes only a first attempt to understand the (at least for us) perplexing complexity of galanin function on the brain.

(2) Calcium imaging is the primary data for the paper, but there are no representative time-series images or movies of GCaMP signal in the various mutants used.

We have now added various movies in supplementary data.

(3) For Figure 3, the authors suggest that hsp70I:gal x eaat2a-/-mutants would further increase galanin transcript levels, which were hypothesized to further reduce brain activity. However, the authors failed to measure galanin transcript levels in this cross to show that galanin is actually increased more than the eaat2a-/- mutant or the hsp70I:gal mutant alone.

After a couple of unsuccessful mating attempts with our older mutants, we finally decided not to wait for a new generation to grow up, deeming the experiment not crucial (but still nice to have).

(4) Similarly, transcript levels of galanin are not provided in Figure 2 for Gal-/- mutants and galr1a KOs. Transcript levels would help validate the knockout and any potential compensatory effects of subtype-specific knockout.

To validate the gal-/- mutant line, we decided to show loss of protein expression (Suppl. Figure 2), which we deem to more relevant to argue for loss of function. Galanin transcript levels in galr1a KOs were also added into the same Figure. However, validation of the galr1a KO could not be performed due to transcript levels being close to the detection limit and lack of available antibodies.

(5) The authors very heavily rely on calcium imaging of different mutant lines. Additional methods could strengthen the data, translational relevance, and interpretation (e.g., acute pharmacology using galanin agonists or antagonists, brain or cell recordings, biochemistry, etc).

Again, we agree and concede that a number of additional approaches are needed to get more insight into the complex role of galanin in regulation overall brain activity. These include, among others, also behavioral, multiple single cell recordings and pharmacological interventions.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Minor issues:

(1) "Sedative" effect of galanin is somewhat vague and seems overapplied without the inclusion of behavioral data showing sedation effects. I would replace "sedative" with something clearer, like the phrase "net inhibitory effect" or similar.

We have modified the wording as deemed appropriate.

(2) Include new data that is sufficiently powered to detect or rule out the effects of sex as a biological variable within the various experiments.

At this stage sex is not a biological variable. Sex determination starts a late larval stage around 14dpf. Our analysis is based on 5pdf larvae.

(3) Attempt to perform some experiments with galanin/galr1a manipulations that have been induced after the majority of development without using heat shock induction if possible (unknown how feasible this is in current model systems).

In the current model this is not feasible, but an excellent suggestion for future studies that would then also address more longterm effects in the model.

(4) Figure 2 should include qPCR results for galanin or galr1a mRNA expression to match Figure 1C, F, and Figure 2C and to confirm reductions in the respective RNA transcript levels of gal or galr1a. It could be useful to perform qPCR for galanin in all galr1aKO mice to ascertain whether compensatory elevations in galanin occur in response to galr1aKO.

(5) Axes should be made with bolder lines and bolder/larger fonts for readability and consistency throughout.

Indeed, an excellent suggestion. We have adjusted the axes significantly improving the readability of the graphs.

(6) The bottom o,f the image for Figure 2 appears to have been cut off by mistake (page 5).

(7) The ending of the legend text for Figure 3 appears to have been cut off by mistake (page 6).

Both regrettable mistakes have been corrected (already in the initial posted version)

Reviewer #3 (Recommendations For The Authors):

(1) The introduction or first paragraph of the results should be revised to more directly state the hypotheses. Several critical details were only clear after reading the discussion.

We added some words to the introduction, hoping that the critical points are now more apparent to the reader.

(2) Galanin is known to be rapidly depleted by seizures (Mazarati et al., 1998; Journal of Neuroscience, PMID #9822761) but this paper did not appear to be cited or considered. Could the rapid depletion of galanin during seizures help explain the confusing effects of galanin manipulations during PTZ?

We have added a sentence and the reference to the discussion.

(3) Figure 1 panels are incorrect. For example, Panel 'F' is used twice and the figure legend is also incorrect due to the labeling errors. In-text references to the figure should also be updated accordingly.

(4) In Figure 2 N-P, the delta F/F threshold wording is partially cropped. The figure should be updated.

Thank you for pointing out this mistake. Both figures have now been updated (already in the initial posted version)

(5) The naming and labeling of groups in the manuscript and figures should be updated to more accurately reflect the fish used for each experiment. As it currently stands, I found the labeling confusing and sometimes misleading. For example, Figure 3 'controls' are actually eaat2a-/- mutants, whereas the other group is hsp70I:gal x eaat2a-/- crosses or gal-/- x eaat2a-/- crosses. In other Figures, 'controls' are eaat2a+/+larva, or wild-type siblings (sometimes unclear).

We have made appropriate changes to the manuscript to make this point clearer to the reader, especially when the controls are eaat2a mutants.

(6) Figure 4J and 4K only show 5 data points, when the authors clearly indicate that 6 fish had seizures. Continuation of this data in Figure 4L shows 6 data points.

Indeed the 6 data points in Figure 4J and K are hard to see due to their nearly complete overlap. On larger magnification all six data points become distinguishable. We will try some different plotting approaches for the revision.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

In this valuable study, García-Vázquez et al. provide solid evidence suggesting that G2 and S phases expressed protein 1 (GTSE1), is a previously unappreciated non-pocket substrate of cyclin D1-CDK4/6 kinases. To this end, this study holds a promise to significantly contribute to an improved understanding of the mechanisms underpinning cell cycle progression. Notwithstanding these clear strengths of the article, it was thought that the study may benefit from establishing the precise role of cyclin D1-CDK4/6 kinase-dependent GTSE1 phosphorylation in the context of cell cycle progression, …

We do not claim, as editors and reviewers appear to have interpreted, that GTSE1 is phosphorylated by cyclin D1-CDK4 in the G1 phase of the cell cycle under normal physiologic conditions.  Indeed, we agree with the existing literature indicating that in cells that do not express high levels of cyclin D1, GTSE1 is expressed predominantly during S and G2 phase (hence the name GTSE1, which stands for G-Two and S phases expressed protein 1) and is phosphorylated by mitotic cyclins in early mitosis.  Even during G1, when the levels of cyclin D1 peak, GTSE1 is not phosphorylated in normal cells.  This could be due to either a higher affinity between GTSE1 and mitotic cyclins as compared to D-type cyclins or to a higher concentration of mitotic cyclins compared to D-type cyclins.  In the current manuscript, we show that higher levels of cyclin D1 can drive the sustained phosphorylation of GTSE1 across all cell cycle points. To reach this conclusion, we do not rely only on the overexpression of exogenous cyclin D1. In fact, we observe similar effect when we deplete endogenous AMBRA1, resulting in the stabilization of endogenous cyclin D1 in all cell cycle phases (see Figure 2G and Figure supplement 3B).  As we had already mentioned in the Discussion section, we propose that GTSE1 is phosphorylated by CDK4 and CDK6 particularly in pathological states, such as cancers displaying overexpression of D-type cyclins (i.e., it is possible that the overexpression overcomes the lower affinity of the cyclin D-GTSE1 complex). In turn, phosphorylation of GTSE1 induces its stabilization, leading to increased levels that, as expected based on the existing literature, contribute to enhanced cell proliferation.  So, the role of the cyclin D1-CDK4/6 kinase-dependent GTSE1 phosphorylation is to stabilize GTSE1 independently of the cell cycle.  In sum, our study suggests that overexpression of cyclin D1, which is often observed in cancers cells beyond the G1 phase, induces phosphorylation of GTSE1 at all points in the cell cycle. 

… obtaining more direct evidence that cyclin D1-CDK4/6 kinase phosphorylate indicated sites on GTSE1 (e.g., S454) …

We show that treatment of cells with palbociclib completely abolished the effect of cyclin D1-CDK4 on the GTSE1 shift observed using Phos-tag gels (Figure 2H).  Moreover, mutagenesis analysis shows that S91, S262, and S724 are phosphorylated in a cyclin D1-CDK4-dependent manner (Figure 2F and Figure supplement 3A). Compared to wild-type GTSE1, a triple mutant (S91A/S262A/S724A) displayed loss of slower-migrating bands upon co-expression of cyclin D1-CDK4, suggesting diminished phosphorylation. Nevertheless, a residual slow-migrating band persisted, prompting further mutations of the triple GTSE1 mutant in S331 and S454 (individually), which do not have a CDK-phosphorylation consensus, but were identified in several published phospho-proteomics studies. From these two quadruple mutants, only the that containing the S454A mutation demonstrated a complete abrogation of any shift in phos-tagTM gels (Figure 2F). These studies suggest that four major sites (S91, S262, S454, and S724) are phosphorylated (either directly and/or indirectly) in a cyclin D1-CDK4-dependent manner.

… and mapping a degron in GTSE1 whose function may be blocked by cyclin D1-CDK4/6 kinase-dependent phosphorylation.

We show that stabilization or overexpression of cyclin D1, which is often observed in human cancers, promotes GTSE1 phosphorylation on S91, S262, S454, and S724, resulting in GTSE1 stabilization.  Similarly, a phospho-mimicking mutant with the 4 serine residues replaced with an aspartate at positions 91, 261, 454, and 724 display increased half-life. While we appreciate the editor’s suggestion and agree on these being interesting questions, we would like to respectfully point out that mapping the GTSE1 degron and understanding how it is affected by cyclin D1-CDK4/6-dependent phosphorylation is outside the scope of the current project and will require an extensive set of experiments and tools. Accordingly, the three reviewers did not ask to map the GTSE1 degron.  We plan on addressing these interesting questions as part of a follow-up study.

Reviewer #1 (public review):

Summary:

García-Vázquez et al. identify GTSE1 as a novel target of the cyclin D1-CDK4/6 kinases. The authors show that GTSE1 is phosphorylated at four distinct serine residues and that this phosphorylation stabilizes GTSE1 protein levels to promote proliferation.

Strengths:

The authors support their findings with several previously published results, including databases. In addition, the authors perform a wide range of experiments to support their findings.

Weaknesses:

I feel that important controls and considerations in the context of the cell cycle are missing. Cyclin D1 overexpression, Palbociclib treatment and apparently also AMBRA1 depletion can lead to major changes in cell cycle distribution, which could strongly influence many of the observed effects on the cell cycle protein GTSE1. It is therefore important that the authors assess such changes and normalize their results accordingly.

We have approached the question of GTSE1 phosphorylation to account for potential cell cycle effects from multiple angles: 

(i) We conducted in vitro experiments with purified, recombinant proteins and shown that GTSE1 is phosphorylated by cyclin D1-CDK4 in a cell-free system (Figure 2A-C). These experiments provide direct evidence of GTSE1 phosphorylation by cyclin D1-CDK4 without the influence of any other cell cycle effectors. 

(ii) We present data using synchronized AMBRA1 KO cells (new Figure 2G and Figure supplement 3B).  In agreement with what we had shown previously (Simoneschi et al., Nature 2021, PMC8875297), AMBRA1 KO cells progress faster in the cell cycle but they are still synchronized as shown, for example, by the mitotic phosphorylation of Histone H3, peaking at 32 hours after serum readdition like in parental cells. Under these conditions we observed that while phosphorylation of GTSE1 in parental cells is evident in the last two time points, AMBRA1 KO cells exhibited sustained phosphorylation of GTSE1 across all cell cycle phases.  This was evident enough when using Phos-tag gels as in the top panel of the old Figure 2G. We now re-run one the biological triplicates of the synchronized cells using higher concentration of Zn⁺²-Phos-tag reagent and lower voltage to allow better separation of the phosphorylated bands.  Under these conditions, GTSE1 phosphorylation is better appreciable (top panel of the new Figure 2G). This experiment provides evidence that high levels of cyclin D1 in AMBRA1 KO cells affect GTSE1 phosphorylation independently of the specific points in the cell cycle. 

(iii) The relative short half-life of GTSE1 (<4 hours) makes its levels sensitive to acute treatments such as Palbociclib or acute AMBRA1 depletion. The effects of these treatments on GTSE1 levels are measurable within a time frame too short to significantly affect cell cycle progression. For example, we used cells with fusion of endogenous AMBRA1 to a mini-Auxin Inducible Degron (mAID) at the N-terminus. This system allows for rapid and inducible degradation of AMBRA1 upon addition of auxin, thereby minimizing compensatory cellular rewiring. Again, we observed an increase in GTSE1 levels upon acute ablation of AMBRA1 (i.e., in 8 hours) (Figure 3B), when no significant effects on cell cycle distribution are observed (please see Simoneschi et al., Nature 2021, PMC8875297 and Rona et al., Mol. Cell 2024, PMC10997477).

Altogether, the above lines of evidence support our conclusion that GTSE1 is a target of cyclin D1-CDK4, independent of cell cycle effects.

In conclusion, we do not claim that GTSE1 is phosphorylated by cyclin D1-CDK4 in the G1 phase of the cell cycle under normal physiologic conditions.  Indeed, we agree with the existing literature indicating that in cells that do not express high levels of cyclin D1, GTSE1 is expressed predominantly during S and G2 phase (hence the name GTSE1, which stands for G-Two and S phases expressed protein 1) and is phosphorylated by mitotic cyclins in early mitosis.  Even during G1, when the levels of cyclin D1 peak, GTSE1 is not phosphorylated in normal cells. This could be due to either a higher affinity between GTSE1 and mitotic cyclins as compared to D-type cyclins or to a higher concentration of mitotic cyclins compared to D-type cyclins.  In the current manuscript, we show that higher levels of cyclin D1 can drive the sustained phosphorylation of GTSE1 across all cell cycle points. To reach this conclusion, we do not rely only on the overexpression of exogenous cyclin D1. In fact, we observe similar effect when we deplete endogenous AMBRA1, resulting in the stabilization of endogenous cyclin D1 in all cell cycle phases (see Figure 2G and Figure supplement 3B).  As we had already mentioned in the Discussion section of the original submission, we propose that GTSE1 is phosphorylated by CDK4 and CDK6 particularly in pathological states, such as cancers displaying overexpression of D-type cyclins (i.e., it is possible that the overexpression overcomes the lower affinity of the cyclin D1-GTSE1 complex). In turn, phosphorylation of GTSE1 induces its stabilization, leading to increased levels that, as expected based on the existing literature, contribute to enhanced cell proliferation.  In sum, our study suggests that overexpression of cyclin D1, which is often observed in cancers cells beyond the G1 phase, induces phosphorylation of GTSE1 at all points in the cell cycle.    

Reviewer #2 (public review):

Summary:

The manuscript by García-Vázquez et al identifies the G2 and S phases expressed protein 1(GTSE1) as a substrate of the CycD-CDK4/6 complex. CycD-CDK4/6 is a key regulator of the G1/S cell cycle restriction point, which commits cells to enter a new cell cycle. This kinase is also an important therapeutic cancer target by approved drugs including Palbocyclib. Identification of substrates of CycD-CDK4/6 can therefore provide insights into cell cycle regulation and the mechanism of action of cancer therapeutics. A previous study identified GTSE1 as a target of CycB-Cdk1 but this appears to be the first study to address the phosphorylation of the protein by Cdk4/6.

The authors identified GTSE1 by mining an existing proteomic dataset that is elevated in AMBRA1 knockout cells. The AMBRA1 complex normally targets D cyclins for degradation. From this list, they then identified proteins that contain a CDK4/6 consensus phosphorylation site and were responsive to treatment with Palbocyclib.

The authors show CycD-CDK4/6 overexpression induces a shift in GTSE1 on phostag gels that can be reversed by Palbocyclib. In vitro kinase assays also showed phosphorylation by CDK4. The phosphorylation sites were then identified by mutagenizing the predicted sites and phostag got to see which eliminated the shift.

The authors go on to show that phosphorylation of GTSE1 affects the steady state level of the protein. Moreover, they show that expression and phosphorylation of GTSE1 confer a growth advantage on tumor cells and correlate with poor prognosis in patients.

Strengths:

The biochemical and mutagenesis evidence presented convincingly show that the GTSE1 protein is indeed a target of the CycD-CDK4 kinase. The follow-up experiments begin to show that the phosphorylation state of the protein affects function and has an impact on patient outcomes.

Weaknesses:

It is not clear at which stage in the cell cycle GTSE1 is being phosphorylated and how this is affecting the cell cycle. Considering that the protein is also phosphorylated during mitosis by CycB-Cdk1, it is unclear which phosphorylation events may be regulating the protein.

Please see point (ii) and the last paragraph in the response to Reviewer #1.  Moreover, we show that, compared to the amino acids phosphorylated by cyclin D1-CDK4, cyclin B1-CDK1 phosphorylates GTSE1 on either additional residues or different sites (Figure 2H). We also show that expression of a phospho-mimicking GTSE1 mutant leads to accelerated growth and an increase in the cell proliferative index (Figure 4B,C and new Figure supplement 4D-E).  Finally, we have evaluated also the cell cycle distributions by flow cytometry (new Figure supplement 4F). These analyses show that the expression of a phospho-mimicking GTSE1 mutant induces a decrease in the percentage of cells in G1 and an increase in the percentage of cells in S, similarly to what observed in AMBRA1 KO cells.

Reviewer #3 (public review)

Summary:

This paper identifies GTSE1 as a potential substrate of cyclin D1-CDK4/6 and shows that GTSE1 correlates with cancer prognosis, probably through an effect on cell proliferation. The main problem is that the phosphorylation analysis relies on the over-expression of cyclin D1. It is unclear if the endogenous cyclin D1 is responsible for any phosphorylation of GTSE1 in vivo, and what, if anything, this moderate amount of GTSE1 phosphorylation does to drive proliferation.

Strengths:

There are few bonafide cyclin D1-Cdk4/6 substrates identified to be important in vivo so GTSE1 represents a potentially important finding for the field. Currently, the only cyclin D1 substrates involved in proliferation are the Rb family proteins.

Weaknesses:

The main weakness is that it is unclear if the endogenous cyclin D1 is responsible for phosphorylating GTSE1 in the G1 phase. For example, in Figure 2G there doesn't seem to be a higher band in the phos-tag gel in the early time points for the parental cells. This experiment could be redone with the addition of palbociclib to the parental to see if there is a reduction in GTSE1 phosphorylation and an increase in the amount in the G1 phase as predicted by the authors' model. The experiments involving palbociclib do not disentangle cell cycle effects. Adding Cdk4 inhibitors will progressively arrest more and more cells in the G1 phase and so there will be a reduction not just in Cdk4 activity but also in Cdk2 and Cdk1 activity. More experiments, like the serum starvation/release in Figure 2G, with synchronized populations of cells would be needed to disentangle the cell cycle effects of palbociclib treatment.   

Please see last paragraph in the response to Reviewer #1.  Concerning the experiments involving palbociclib, we limited confounding effects on the cell cycle by treating cells with palbociclib for only 4-6 hours. Under these conditions, there is simply not enough time for S and G2 cells to arrest in G1.

It is unclear if GTSE1 drives the G1/S transition. Presumably, this is part of the authors' model and should be tested.

We are not claiming that GTSE1 drives the G1/S transition (please see last paragraph in the response to Reviewer #1). GTSE1 is known to promote cell proliferation, but how it performs this task is not well understood.  Our experiments indicate that, when overexpressed, cyclin D1 promotes GTSE1 phosphorylation and its consequent stabilization.  In agreement with the literature, we show that higher levels of GTSE1 promote cell proliferation.  To measure cell cycle distribution upon expressing various forms of GTSE1, we have now performed FACS analyses (new Figure supplement 4F). These analyses show that the expression of a phospho-mimicking GTSE1 mutant induces a decrease in the percentage of cells in G1 and an increase in the percentage of cells in S, similarly to what observed in AMBRA1 KO cells shown in the same panel and in Simoneschi et al. (Nature 2021, PMC8875297).

The proliferation assays need to be more quantitative. Figure 4B should be plotted on a log scale so that the slope can be used to infer the proliferation rate of an exponentially increasing population of cells. Figure 4c should be done with more replicates and error analysis since the effects shown in the lower right-hand panel are modest.

In Figure 4B, we plotted data in a linear scale as done in the past (Donato et al. Nature Cell Biol. 2017, PMC5376241) to better underline the changes in total cell number overtime.  The experiments in Figure 4B were performed in triplicate, statistical significance was determined using unpaired T-tests with p-values<0.05, and error bars represent the mean +/- SEM.  In Figure 4C, error analysis was not included for simplicity, given the complexity of the data.  We have now included the other two sets of experiments (new Figure supplement 4D,E).  While the effects shown in the lower right-hand panel of Figure 4C are modest, they demonstrate the same trend as those observed in the AMBRA KO cells (Figure 4C and Simoneschi et al., Nature 2021, PMC8875297). It's important to note that this effect is achieved through the stable expression of a single phospho-mimicking protein, whereas AMBRA KO cells exhibit changes in numerous cell cycle regulators. Moreover, these effects are obtained by growing cells in culture for only 5 days. A similar impact on cell growth in vivo over an extended period could pose significant risks in the long term.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Figure 1E is referenced before 1D. The authors should consider switching D and E.

Done.

Figure 1D-E: The authors correctly note in the introduction that GTSE1 is encoded by a cell cycle-dependently expressed gene. Given that cell cycle genes are often associated with poor prognosis (e.g., see Whitfield et al., 2006 Nat. Rev. Cancer), this would be expected to correlate with poor prognosis. This should be mentioned in the results section.

We agree that the overexpression of certain (but not all) cell cycle-regulated genes are prognostically unfavorable across various cancer types, and we cited Whitfield et al., 2006 Nat. Rev. Cancer.  However, our data indicate that phosphorylation of GTSE1 induces its stabilization and, consequently, its levels do not oscillate during the cell cycle any longer (new Figure 2G and Figure supplement 3B).  Moreover, analyzing data from the Clinical Proteomic Tumor Analysis Consortium, we observed an enrichment of GTSE1 phospho-peptides (normalized to total protein) within a pan-cancer cohort as opposed to adjacent, corresponding normal tissues (Figure 2I).

Figure 2F: Contrast is too high. Blot images should not contain fully saturated black or white.

We corrected the contrast.

Figure 2G and Figure Supplement 3B: It looks like AMBRA1 KO cells do not synchronize properly in response to serum withdrawal. The cell cycle distribution should be checked by FACS. Otherwise, it is unclear whether changes in GTSE1 (phosphor) levels are only due to indirect changes in the cell cycle distribution.

Synchronization of both parental and AMBRA1 KO cells is demonstrated by the fact that the phosphorylation of Histone H3 peaks at 32 hours after serum readdition in both cases (Figure supplement 3B). 

Figure 2I: It is important that phosphor-GTSE1 levels are normalized to total GTSE1 levels to understand the distinct contribution of changes in GTSE1 levels and from CCND1-CDK4 driven phosphorylation.

Done.

Figure 3A-B: These experiments should also be controlled for cell cycle distribution. Is this effect specific to GTSE1 and other AMBRA1 targets or are other G2/M cell cycle proteins also affected?

The relative short half-life of GTSE1 (<4 hours) makes its levels sensitive to acute treatments such as Palbociclib or acute AMBRA1 depletion. The effects of these treatments on GTSE1 levels are measurable within a time frame too short to significantly affect cell cycle progression. For example, we used cells with fusion of endogenous AMBRA1 to a mini-Auxin Inducible Degron (mAID) at the N-terminus. This system allows for rapid and inducible degradation of AMBRA1 upon addition of auxin, thereby minimizing compensatory cellular rewiring. Again, we observed an increase in GTSE1 levels upon acute ablation of AMBRA1 (i.e., in 8 hours) (Figure 3B), when no significant effects on cell cycle distribution are observed (please see Simoneschi et al., Nature 2021, PMC8875297 and Rona et al., Mol. Cell 2024, PMC10997477).

Figure 4: It should be noted that the correlation with cell proliferation and cell cycle protein expression is expected for any cell cycle protein, including GTSE1.

Actually, the main point of Figure 4 is to show that expression of the phospho-mimicking mutant of GTSE1 promotes cell proliferation. Comparative analysis revealed that cells overexpressing either wild-type GTSE1 or its phospho-deficient form exhibited significantly reduced proliferation rates compared to those expressing the phospho-mimicking mutant (Figure 4B,C). 

The two-decades-old references 33 and 34 are not well suited to support the notion for Cyclin D1 that "the full spectrum of substrates and their impact on cellular function and oncogenesis remain poorly explored." More recent references should be used to show that this is still the case.

We added more recent references.

The authors conclude that their "data indicate that cyclin D1-CDK4 is responsible for the phosphorylation of GTSE1 on four residues (S91, S262, S454, and S724)." However, the authors' data do not exclude a role for their siblings cyclin D2, cyclin D3, and CDK6. Reflecting this, the conclusions should be toned down.

The analysis of the sites phosphorylated in GTSE1 was performed by experimentally co-expressing cyclin D1-CDK4 (Figure 2F, Figure 2H, and Figure supplement 3A), hence our statement.  Yet, we agree that in cells, cyclin D2, cyclin D3, and CDK6 can contribute to GTSE1 phosphorylation. 

The authors claim that they "observed that in human cells, when D-type cyclins are stabilized in the absence of AMBRA1, GTSE1 becomes phosphorylated also in G1." However, the G1-specific data presented by the authors are not controlled for, and it is unclear whether these phosphorylation events actually occur in G1 cells.

We now provide a WB in which GTSE1 phosphorylation is more evident (top panel of the new Figure 2G) (please see point (ii) in the response to the public review of Reviewer #1).  This experiment clearly shows that in AMBRA1 KO cells, GTSE1 is phosphorylated at all points in the cell cycle. Synchronization of both parental and AMBRA1 KO cells is demonstrated by the fact that phosphorylation of Histone H3 peaks at 32 hours after serum re-addition in both cases (Figure supplement 3B). 

Reviewer #2 (Recommendations for the authors):

(1) It is not clear from the presented data at which point in the cell cycle that phosphorylation of GTSE1 may be affecting the steady state level of the protein. The implication that GTSE1 is a target of CycD-CDK4 would suggest that the protein is stabilized at G1/S. Can this effect be observed?

Please see the last paragraph in the response to the public review of Reviewer #1.

(2) Considering the previous study showing that GTSE1 is also phosphorylated during mitosis by CycB-Cdk1, do levels of GTSE1 protein change during the cell cycle? Do changes in GTSE1 levels correlate with phosphorylation during the cell cycle? Cell synchronization experiments such as double thymidine and subsequent phostag analysis could shed some light on these questions.

Please see the last paragraph in the response to the public review of Reviewer #1.

(3) The authors show that the phosphomimetic mutants of GTSE1 confer a growth advantage on cells. The mechanism of this growth advantage is unclear. Is this effect due to a shorter cell cycle, enhanced survival, or another mechanism?

We did not observe increased cell survival when the phosphomimetic mutants of GTSE1 is expressed.  We show that phosphorylation of GTSE1 induces its stabilization, leading to increased levels that, as expected based on the existing literature, contribute to enhanced cell proliferation.  So, the role of the cyclin D1-CDK4/6 kinase-dependent phosphorylation of GTSE1 is to stabilize GTSE1. 

(4) Other minor points - all of the presented immunoblots do not show molecular weight markers. The IF images require scale bars.

To prevent overcrowding of the Figures, the sizes of blotted proteins are indicated in the uncropped scans of each blot. Uncropped scans have been deposited in Mendeley at:  https://data.mendeley.com/datasets/xzkw7hrwjr/1. Scale bars have been added to the IF images.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper, the authors have leveraged Single-cell RNA sequencing of the various stages of the evolution of lung adenocarcinoma to identify the population of macrophages that contribute to tumor progression. They show that S100a4+ alveolar macrophages, active in fatty acid metabolic activity, such as palmitic acid metabolism, seem to drive the atypical adenomatous hyperplasia (AAH) stage. These macrophages also seem to induce angiogenesis promoting tumor growth. Similar types of macrophage infiltration were demonstrated in the progression of the human lung adenocarcinomas.

Strengths:

Identification of the metabolic pathways that promote angiogenesis-dependent progression of lung adenocarcinomas from early atypical changes to aggressive invasive phenotype could lead to the development of strategies to abort tumor progression.

We are grateful for your constructive comments. These comments are very helpful for revising and improving our paper and have provided important guiding significance to our study. We have made revisions according to your comments and have provided point-by-point responses to your concerns.

Weaknesses:

(1) Can the authors demonstrate what are the functional specialization of the S100a4+ alveolar macrophages that promote the progression of the AAH to the more aggressive phenotype? What are the factors produced by these unique macrophages that induce tumor progression and invasiveness?

Thank you for your comments. To more comprehensively characterize the functional specialization of the S100a4⁺ alveolar macrophages, we expanded the macrophage functional gene sets based on relevant literature and databases and performed enrichment analysis. The results showed that all stages of precancerous progression presented activated states of angiogenesis, M2-like and immunosuppressive functions relative to the normal stage (Figure 4B). As we have demonstrated, S100a4⁺ alveolar macrophages predominantly exert pro-angiogenic functions during the AAH phase and may be more biased towards M2-like polarization and immunosuppression during further disease progression. Consistently, S100A4⁺ subset population of macrophages has been proved to exhibit a M2-like phenotype with immunosuppressive properties in tumor progression [PMID: 34145030]. In addition, S100A4 has been reported to be associated with macrophage M2 polarization, angiogenesis, and tumorigenesis [PMID: 39664586, 36895491, 30221056, 32117590]. The functional status of human S100A4⁺ alveolar macrophages is basically the same. The relevant description was added to the Results section as follows: “It was revealed that the capacities for angiogenesis, M2-like polarization, and immunosuppression were found to be stronger in AAH or other precancerous stages relative to the normal stage (Figure 4B). The pro-angiogenic function predominated in the AAH stage, while M2-like and immunosuppressive functions were more prominent in the subsequent precancerous progression.” (page 11, line 262). Our study puts more attention on the functional phenotypic changes of S100a4⁺ alveolar macrophages during the progression from normal to AAH to explain the role of this subpopulation in tumor initiation, and similarly, preliminary coculture experiments could only indicate its role in the early malignant transformation of epithelial cells. In further experimental validation, we will confirm the above functions of the S100a4⁺ alveolar macrophages promoting the progression of AAH to the more aggressive phenotype by in vitro and in vivo experiments. We have extended the limitations and potential experimental designs to the Discussion section as follows: “It is worth noting that our mining of S100a4⁺ alv-macro remains at the precancerous initiation stage, and further experimental designs are needed to verify its specific contribution at more aggressive stages. For example, FACS sorting of the subpopulation at different stages of disease progression, respectively, for precise functional characterization;” (page 19, line 468).

For the factors produced by these unique macrophages during induction of malignant transformation, we assayed culture supernatant of S100a4-OE alveolar macrophages for secreted functional cytokines. The results showed up-regulation of MIP-2, HGF, TNFα, IL-1a, CD27, CT-1, MMP9, 4-1BB, and CD40, and GO enrichment showed angiogenesis and tumorigenesis-related processes (Figure 5L and 5M). We have added the detailed content to the Results section as follows: “Next, we detected tumor-inducing factors secreted by these unique macrophages using Cytokine Antibody Array. We noted the production of macrophage inflammatory protein (MIP)-2, hepatocyte growth factor (HGF), tumor necrosis factor α (TNF-α), IL-1α, MMP9, and CD40, and these cytokine-related biological processes were mainly involved in the regulation of angiogenesis and immune response (Figure 5L and 5M).” (page 13, line 319). Furthermore, changes in these cytokines during subsequent invasive tumor progression will also be continuously monitored. The description in the Discussion section have been added as: “Furthermore, TGF-β and HGF activate vascular endothelial cells and promote proliferation and migration, as well as induce the expression of pro-angiogenic factors such as VEGF (Vimalraj, 2022; Watabe, Takahashi, Pietras, & Yoshimatsu, 2023). Macrophage-derived TNF-α and IL-1α lead tumor cells to produce potent angiogenic factors IL-8 and VEGF, which affect angiogenesis and tumor growth (Torisu et al., 2000). MIP2 and CD40 were also identified as pro-tumor factors associated with angiogenesis (Kollmar, Scheuer, Menger, & Schilling, 2006; Murugaiyan, Martin, & Saha, 2007)…continuous monitoring of the fluctuation of the above factors in bronchoalveolar lavage fluid at corresponding periods;” (page 19, line 461).

All method details covered in this section have been updated in the Materials and methods.

(2) Angiogenic factors are not only produced by the S100a4+ cells but also by pericytes and potentially by the tumor cells themselves. Then, how do these factors aberrantly trigger tumor angiogenesis that drives tumor growth?

Thank you for your comment. In our study, we detected up-regulation of angiogenic factors HIF-1α, VEGF, MMP9, and TGF-β (Figure 5K), and elevation of secreted HGF, IL-1α, and TNF-α (Figure 5L). We provide a detailed description of how these factors are involved in angiogenesis-related tumorigenesis to varying degrees in the Discussion section: “Precancerous lesions of LUAD are angiogenic, and pro-angiogenic factors secreted by cells, including S100a4⁺ alv-macro, induce endothelial cell sprouting and chemotaxis, leaving the angiogenic switch activated, prompting the formation of new blood vessels on the basis of the original ones to supply oxygen and nutrients to sustain tumor initiation (Chen et al., 2024; Kayser et al., 2003; van Hinsbergh & Koolwijk, 2008). Under hypoxic conditions, HIF-1α activates numerous factors that contribute to the angiogenic process, including VEGF, which promotes vascular permeability, and MMP9, which breaks down the ECM, promotes endothelial cell migration, and recruits pericytes to provide structural support (Raza, Franklin, & Dudek, 2010; Sakurai & Kudo, 2011). Cytokines secreted into the microenvironment activate macrophages, which subsequently produce angiogenic factors, further promoting angiogenesis (Sica, Schioppa, Mantovani, & Allavena, 2006). Furthermore, TGF-β and HGF activate vascular endothelial cells and promote proliferation and migration, as well as induce the expression of pro-angiogenic factors such as VEGF (Vimalraj, 2022; Watabe, Takahashi, Pietras, & Yoshimatsu, 2023). Macrophage-derived TNF-α and IL-1α lead tumor cells to produce potent angiogenic factors IL-8 and VEGF, which affect angiogenesis and tumor growth (Torisu et al., 2000)…” (page 19, line 449).

(3) It is not clear how abnormal fatty acid uptake by the macrophages drives the progression of tumors.

Thank you for your comment, which coincides with our mechanistic exploration. The metabolic status of macrophages influences their pro-tumor properties, and lipid metabolism has been shown to determine the functional polarization of macrophages [PMID: 29111350]. In this study, we observed more accumulation of lipid droplets in S100a4-OE MH-S, demonstrating enhanced cellular fatty acid uptake (Figure 6A). The pro-angiogenic ability of S100a4⁺ alv-macro was confirmed by tube formation assay and cytokine assay (Figure 6B and 5M). Cpt1a was thought to play a crucial role in the metabolic paradigm shift of S100a4⁺ alv-macro, we therefore performed functional rescue experiments by inhibiting CPT1A expression in S100a4-OE MH-S by addition of etomoxir (ETO). After culture with conditioned medium of MH-S, the proliferation, migration, and ROS production of MLE12 cells were all restored to lower levels (Figure 6E-G). In addition, ETO treatment significantly reversed the angiogenesis, which supported the regulation of fatty acid metabolism on macrophage function (Figure 6H). Immunoblotting also revealed restoration of expression in related proteins (Figure 6I and 6J), these findings reinforced previous analyses of the association of fatty acid metabolism with pro-angiogenesis and M2-like function in S100a4⁺ alv-macro. The involvement of PPAR-γ in the regulation of metabolic state was also confirmed. Taken together, we suggest that S100a4⁺ alv-macro promotes fatty acid metabolism through the CPT1A-PPAR-γ axis, enhances its ability to promote angiogenesis, and thus drives tumor occurrence. The corresponding contents were added in the Results section S100a4⁺ alv-macro drove angiogenesis by promoting Cpt1a-mediated fatty acid metabolism (page 13, line 327) and Discussion section: “We demonstrated the regulation of fatty acid metabolism by CPT1A in S100a4⁺ alv-macro as well as the involvement of PPAR-γ. Nevertheless, the molecular mechanism that drives the acquisition of metabolic and functional switching properties specific to this cell state still requires further characterization in the context of precancerous lesions. It has been reported that CD36 is the main effector of the S100A4/PPAR-γ pathway, and its mediated fatty acid uptake plays an important role in the tumor-promoting function of macrophages (S. Liu et al., 2021).” (page 18, line 433).

All method details covered in this section have been supplemented in the Materials and methods.

(4) Does infusion or introduction of S100a4+ polarized macrophages promote the progression of AAH to a more aggressive phenotype?

Thank you for your comment. We performed intratracheal instillation of lentivirus-infected S100a4-OE MH-S and culture supernatant in A/J and BALB/c mice, respectively, but no aggressive pathological phenotype was observed so far, possibly due to the lack of time required for lesions or the imperfection of experimental conditions. We will continue to explore the instillation dose and frequency for long-term monitoring and will simultaneously evaluate the availability of primary alveolar macrophages. We have discussed as follows: “It is worth noting that our mining of S100a4⁺ alv-macro remains at the precancerous initiation stage, and further experimental designs are needed to verify its specific contribution at more aggressive stages…and intratracheal instillation of primary S100a4⁺ alv-macro to observe the pathological progression of precancerous lesions.” (page 19, line 468).

(5) How does Anxa and Ramp1 induction in inflammatory cells induce angiogenesis and tumor progression?

Thank you for your comment. ANXA2 is an important member of annexin family of proteins expressed on surface of endothelial cells, macrophages, and tumor cells [PMID: 30125343]. ANXA2 was reported to regulate neoangiogenesis in the tumor microenvironment and most likely due to overproduction of plasmin. As a well-established receptor for plasminogen (PLG) and tissue plasminogen activator (tPA) on the cell surface, ANXA2 converts PLG into plasmin. Plasmin plays a critical role in the activation of cascade of inactive proteolytic enzymes such as metalloproteases (pro-MMPs) and latent growth factors (VEGF and bFGF) [PMID: 12963694, 11487021]. Activated forms of MMPs and VEGF then induce extracellular matrix remodeling facilitating angiogenesis and tumor development [PMID: 15788416]. Sharma et al. suggested administration of ANXA2-antibody inhibited tumor angiogenesis and growth concurrent with plasmin generation [PMID: 22044461], the role of ANXA2 in plasmin activation thus explains it’s importance in tumor-related angiogenesis. We verified the simultaneous upregulation of ANXA2 and PLG in S100a4-OE MH-S and cocultured HUVEC and MLE12 by immunoblotting (Figure 6D). The relevant description was added to the Results section as follows: “ANXA2 is considered to be a cellular receptor for plasminogen (PLG), often expressed on the surface of endothelial cells, macrophages, and tumor cells, which activates a cascade of pro-angiogenic factors by promoting the conversion of PLG to plasmin, thereby promoting angiogenesis and tumor progression (Semov et al., 2005; Sharma, 2019). We found synergistic upregulation of ANXA2 and PLG expression in S100a4-OE MH-S and cocultured HUVEC and MLE12, which may help explain how ANXA2 induction was involved in angiogenesis and malignant transformation (Figure 6D).” (page 14, line 338).

Recent studies showed that S100A4 is associated with tumor angiogenesis and progression by the interaction with ANXA2. ANXA2 is the endothelial receptor for S100A4 and that their interaction triggers the functional activity directly related to pathological properties of S100A4, including angiogenesis [PMID: 18608216]. It has been proved that S100A4 induces angiogenesis through interaction with ANXA2 and accelerated plasmin formation [PMID: 15788416, 25303710]. In addition, it is generally believed that ANXA2 participates in malignant cell transformation [PMID: 28867585]. Therefore, we speculate that ANXA2 may promote plasmin production by binding to S100A4, thus promoting angiogenesis and tumor initiation, and we have discussed accordingly: “The role of ANXA2 in angiogenesis has been widely recognized, and it may facilitate plasmin production by binding to S100A4 and then trigger angiogenesis and malignant cell transformation (Grindheim, Saraste, & Vedeler, 2017; Y. Liu, Myrvang, & Dekker, 2015).” (page 18, line 446).

In our study, the primary target of our validation was ANXA2 rather than RAMP1, even though its relationship with angiogenesis had been established [PMID: 20596610], so we weakened the relevant description in the manuscript.

(6) For the in vitro studies the authors might consider using primary tumor cells and not cell lines.

Thank you for your suggestion, which was in our initial experimental plan. However, since S100A4 is not expressed on the cell surface, FACS sorting of primary subset of alveolar macrophages presents technical limitations. We have also attempted overexpression in primary macrophages, but the current overexpression efficiency and cell status are not sufficient to support a subsequent series of experiments. For all these reasons, the alveolar macrophage cell line MH-S and the lung epithelial cell line MLE12 were selected to ensure the consistency and stability of the coculture system.

In addition, we are optimizing the experimental conditions to achieve coculture of primary macrophages and epithelial cells, and will also establish transgenic mouse models for simultaneous validation. The Discussion has been added as: “Besides, as our previous in vitro results were obtained based on cell lines, we will optimize the experimental conditions to achieve coculture of primary macrophage subset and epithelial cells and establish transgenic mouse models for in vivo validation.” (page 19, line 475).

Reviewer #2 (Public review):

Summary:

The work aims to further understand the role of macrophages in lung precancer/lung cancer evolution

Strengths:

(1) The use of single-cell RNA seq to provide comprehensive characterisation.

(2) Characterisation of cross-talk between macrophages and the lung precancerous cells.

(3) Functional validation of the effects of S100a4+ cells on lung precancerous cells using in vitro assays.

(4) Validation in human tissue samples of lung precancer / invasive lesions.

We are grateful for your constructive comments. These comments are very helpful for revising and improving our paper and have provided important guiding significance to our study. We have made revisions according to your comments and have provided point-by-point responses to your concerns.

Weaknesses:

(1) The authors need to provide clarification of several points in the text.

Thank you for your comment. We have clarified these points in the manuscript and responded to all your concerns in detail. Please see the responses to Recommendations for the authors.

(2) The authors need to carefully assess their assumptions regarding the role of macrophages in angiogenesis in precancerous lesions.

Thank you for your comment. We have cited relevant literature to support the occurrence of angiogenesis in precancerous lesions, and demonstrated the contribution of S100a4⁺ alveolar macrophages by tube formation assay and cytokine assay. In addition, we have discussed the relevant limitations of this study and aimed to provide more robust evidence. Please see the responses to Recommendations for the authors.

(3) The authors should discuss more broadly the current state of anti-macrophage therapies in the clinic.

Thank you for your suggestion. We have provided extensive discussion of the clinical state of anti-macrophage therapies. Please see the responses to Recommendations for the authors.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The text has grammatical and syntax errors that need to be corrected accordingly.

Thank you for your suggestion. We have corrected the grammatical and syntactic errors and asked a native English speaker in the field to help polish the full text.

Reviewer #2 (Recommendations for the authors):

This work provides an important contribution to our further understanding of the role of macrophages in lung precancer/lung cancer evolution. I have several comments regarding how the manuscript could be improved:

Introduction:

The authors may consider citing the following work to enhance their work:

(1) At line 78, where they talk about precancerous lesions being reversible, they should cite recent work on this in lung cancer: Teixeria et al 2019 PMID: 30664780, and Pennycuik et al 2020 PMID: 32690541.

Thank you for your suggestion. We have cited the above references in the corresponding paragraph (page 4, line 76).

(2) At line 96, where they talk about developing medicines for precancerous lesions, the authors should cite comprehensive review articles where this concept has been discussed in depth, for example: Reynolds et al 2023 PMID: 37067191, and Asad et al 2012 PMID: 23151603.

Thank you for your suggestion. We have cited the above references in the corresponding paragraph (page 5, line 94).

Results:

(1) Line 142, the authors say "mice were feed for 12-16 months" - do they mean the mice were maintained for 12-16 months?

Thank you for your comment. To best mimic the process of human lung cancer development, A/J mice with the highest incidence of spontaneous lung tumors, which increases substantially with age, were selected. The corresponding description has been modified as: “A/J mice have the highest incidence of spontaneous lung tumors among various mouse strains, and this probability significantly increased with age (Landau, Wang, Yang, Ding, & Yang, 1998). To more comprehensively mirror the tumor initiation and progression process of human lung cancer, A/J mice were maintained for 12-16 months for spontaneous lesions, which resulted in three recognizable precancerous lesions in the lung.” (page 7, line 138).

(2) Line 143, the authors claim to have seen "three recognizable precancerous and cancerous lesions in the lung" but then, they only go on to describe AAH, adenoma, and AIS, lesions which are all commonly recognized as precancers. What was the cancerous (i.e. invasive) lesion they identified?

Thank you for your comment. We apologize for this misstatement and will include cancerous lesions from mice for simultaneous analysis in subsequent study. The corresponding description has been revised as: “To more comprehensively mirror the tumor initiation and progression process of human lung cancer, A/J mice were maintained for 12-16 months for spontaneous lesions, which resulted in three recognizable precancerous lesions in the lung.” (page 7, line 140).

(3) Line 172, the authors say that the "proportion of cell types across the four stages showed a dynamic trend" ... what does this mean? A trend towards what exactly?

Thank you for your comment. Our intention was to highlight heterogeneous changes, and the description has been corrected: “The proportion of cell types across the four stages showed irregular changes, while transcriptional homogeneity was reduced with precancerous progression, illustrating the importance of heterogeneity in tumorigenesis and also proving the reliability of the sampling in this study.” (page 8, line 169).

(4) Line 193, the authors say cell communication "showed a tendency to malignant transformation." What does this statement mean? If they mean more cell communication occurred in the malignant lesions than the precancerous, then there is a flaw in the logic because AAH, adenoma, and AIS are all precancerous lesions. What is the sequence of evolution to malignancy the authors are assuming? Do they mean AIS is a more advanced stage of precancerous malignancy than adenoma, and adenoma is more advanced than AAH (albeit they are all precancerous lesions).

Thank you for your comments. The malignant transformation process involves multiple stages, and histological AAH is regarded as the beginning of this process. Precancerous lesions of LUAD in mice are believed to develop stepwise from AAH, adenoma, to AIS, even if the process is not necessarily completely consistent [PMID: 11235908, 32707077]. What we meant to describe was a gradual increase in the frequency of cell communication during this process. The corresponding description has been modified as: “At the evolutionary stages of precancerous LUAD, despite possible sample heterogeneity and other interference, we observed increased interactions between epithelial cells and surrounding stromal and immune cells in the microenvironment, indicating gradually frequent cell-cell communication during this process” (page 8, line 187).

(5) Immunofluorescence images in Figure 3G and Figure 4F are captured at low magnification, making it very difficult to evaluate the colocalisation data. Suggest authors provide higher magnification images.

Thank you for your suggestion. We have replaced the immunofluorescence images in Figure 3G and Figure 4F with higher magnification images.

(6) Line 284 when referencing the cell line here, the author should make it clear in the text that cells were transfected with a construct expressing S100A4. If possible, would be good to understand if the level of S100A4 expression achieved is less, similar, or greater than that seen in these cells in vivo.

Thank you for your suggestion. We have amended the text to make it clear: “S100a4-overexpressed (OE) alveolar macrophages were established by transfection of the mS100a4 vector into the murine MH-S cell line, and empty vector was transfected as negative control (NC) cells” (page 12, line 284), and it will be clarified in the following exploration whether the level of S100a4 expression achieved is less, similar, or greater than that seen in these cells in vivo.

(7) Line 285 - when the authors first refer to OE cells that have been transfected, they should also inform the reader what NC cells are i.e. negative control cells?

Thank you for your suggestion. We have revised the relevant content as follows: “S100a4-overexpressed (OE) alveolar macrophages were established by transfection of the mS100a4 vector into the murine MH-S cell line, and empty vector was transfected as negative control (NC) cells” (page 12, line 284).

(8) Line 324 - the authors claim they have demonstrated that the macrophages promote angiogenesis through upregulation of fatty acid metabolism. Whilst they may have demonstrated changes in fatty acid metabolism, no experiments assessing the effect of the macrophages in angiogenesis assays are included in the paper, so the authors should modify this statement.

Thank you for your comments. The relevant experiments have been added based on your suggestions. Firstly, we demonstrated in vitro the up-regulation of fatty acid metabolism in S100a4⁺ alv-macro and uncovered the contribution of CPT1A to angiogenesis and cell transformation through rescue experiments; Then, HUVEC tube formation assay and cytokine assay confirmed the pro-angiogenic effect of S100a4⁺ alv-macro. We have added the Results section S100a4⁺ alv-macro drove angiogenesis by promoting Cpt1a-mediated fatty acid metabolism (page 13, line 327) and added the Discussion as: “We demonstrated the regulation of fatty acid metabolism by CPT1A in S100a4⁺ alv-macro as well as the involvement of PPAR-γ. Nevertheless, the molecular mechanism that drives the acquisition of metabolic and functional switching properties specific to this cell state still requires further characterization in the context of precancerous lesions. It has been reported that CD36 is the main effector of the S100A4/PPAR-γ pathway, and its mediated fatty acid uptake plays an important role in the tumor-promoting function of macrophages (S. Liu et al., 2021).” (page 18, line 433).

All method details covered in this section have been supplemented in the Materials and methods.

(9) Regarding angiogenesis in precancerous lesions and the role of macrophages in this process: is there even any evidence that precancerous LUAD lesions are angiogenic? Don't these lesions typically have a lepidic pattern, wherein the cancer cells merely co-opt pre-existing alveolar capillaries without the need to generate new vessels?

Thank you for your comments. As you mentioned, pathologically, precancerous LUAD lesions mainly show a lepidic growth pattern, characterized by the growth of type II alveolar epithelial cells along pre-existing alveolar walls [PMID: 29690599], but this does not mean that this process does not require the formation of new blood vessels. There are multiple patterns of tumor angiogenesis. Some studies have shown that increased angiogenesis can be observed in certain precancerous lesions, which suggests that angiogenesis may play an important role in the early stages of lung cancer development. Microvessel density (MVD) was increased in AAH and AIS compared to normal lung tissue, indicating that new blood vessels are forming to provide essential nutrients and oxygen to tumor cells to support their growth. The expression level of pro-angiogenic factors such as VEGF is usually upregulated, which promotes the formation of new blood vessels by stimulating endothelial cell proliferation and migration. [PMID: 39570802, 14568684] In addition, the infiltration of macrophages into precancerous areas in response to cytokines has been shown to trigger a tumor angiogenic switch and maintain tumor-associated continuous angiogenesis [PMID: 35022204]. Our in vitro tube formation assay and cytokine assay also demonstrated angiogenesis induced by S100a4⁺ alv-macro. We have discussed the relevant content (page 19, line 449) and will provide more sufficient evidence in future work.

Discussion:

Perhaps the authors can cite any literature pertaining to the current wave of anti-macrophage therapies currently being tested in the clinic. Moreover, have these therapies been tested in lung cancer, and if so, what were the results?

Thank you for your suggestion. At present, the clinical trials of anti-macrophage therapies mainly involve Gaucher's disease and hematological malignancies, and the two tests related to lung cancer have no valid data posted. Nevertheless, there are some preclinical studies worth learning from. We have cited the relevant literature and discussed in detail: “With the elaborate resolution of TME, macrophage-related therapy is considered to be promising. So far, macrophage-targeted therapy has demonstrated clinical efficacy in Gaucher's disease and advanced hematological malignancies (Barton et al., 1991; Ossenkoppele et al., 2013). In lung cancer, an attempt to enhance anti-PD-1 therapy in NSCLC by depleting myeloid-derived suppressor cells with gemcitabine was prematurely terminated because of insufficient data collected; another clinical trial of TQB2928 monoclonal antibody promoting macrophage phagocytosis of tumor cells in combination with a third-generation EGFR TKI for advanced NSCLC is now recruiting. Moreover, preclinical studies on macrophage-targeted therapy combined with immune checkpoint inhibitors are being extensively conducted in NSCLC, and it was suggested that blockade of purine metabolism can reverse macrophage immunosuppression, and a synergetic effect can be achieved when combined with anti-PD-L1 therapy, which inspired the direction of our early intervention strategies (H. Wang, Arulraj, Anbari, & Popel, 2024; Yang et al., 2025).” (page 20, line 479).

Methods:

Further description of how lesions were classified as precancerous (AAH, adenoma, AIS) or cancerous by the pathologist should be defined (or cite appropriate reference where this is described).

Thank you for your suggestion. We have cited relevant references in the Methods section (page 21, line 528) on how lesions were classified by the pathologists [PMID: 21252716, 28951454, 32707077, 24811831].

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study combines predictions from MD simulations with sophisticated experimental approaches including native mass spectrometry (nMS), cryo-EM, and thermal protein stability assays to investigate the molecular determinants of cardiolipin (CDL) binding and binding-induced protein stability/function of an engineered model protein (ROCKET), as well as of the native E. coli intramembrane rhomboid protease, GlpG.

Strengths:

State-of-the-art approaches and sharply focused experimental investigation lend credence to the conclusions drawn. Stable CDL binding is accommodated by a largely degenerate protein fold that combines interactions from distant basic residues with greater intercalation of the lipid within the protein structure. Surprisingly, there appears to be no direct correlation between binding affinity/occupancy and protein stability.

Weaknesses:

(i) While aromatic residues (in particular Trp) appear to be clearly involved in the CDL interaction, there is no investigation of their roles and contributions relative to the positively charged residues (R and K) investigated here. How do aromatics contribute to CDL binding and protein stability, and are they differential in nature (W vs Y vs F)?

Based on the simulations in Corey et al (Sci Adv 2021), aromatic residues, especially tryptophan, appear to help provide a binding platform for the glycerol moiety of CDL which is quite flat. This interaction is likely why we generally see the tryptophan slightly further into the plane of the membrane than the basic residues, where it may help to orient the lipid. Unlike charge interactions with lipid head groups, such subtle contributions are likely distorted by the transfer to the gas phase, making it difficult to confidently assign changes in stability or lipid occupancy to interactions with tryptophan. We have added an explanation of these considerations to the Discussion section (page 13, last paragraph).

(ii) In the case of GlpG, a WR pair (W136-R137) present at the lipid-water on the periplasmic face (adjacent to helices 2/3) may function akin to the W12-R13 of ROCKET in specifically binding CDL. Investigation of this site might prove to be interesting if it indeed does.

Thank you for the suggestion. In our CG simulations, we don’t see significant CDL binding at this site, likely because there is just a single basic residue. We note that there is a periplasmic site nearby with two basic residues (K132+K191+W125) with a higher occupancy, however still far lower than the identified cytoplasmic site. In general, periplasmic sites are less common and/or have lower affinity which may be related to leaflet asymmetry (Corey et al, Sci Adv 2021). We added the CDL density plot for the periplasmic side to Figure S7 and noted this on page 9, next-to-last paragraph.

(iii) Examples of other native proteins that utilize combinatorial aromatic and electrostatic interactions to bind CDL would provide a broader perspective of the general applicability of these findings to the reader (for e.g. the adenine nucleotide translocase (ANT/AAC) of the mitochondria as well as the mechanoenzymatic GTPase Drp1 appear to bind CDL using the common "WRG' motif.)

Several confirmed examples are presented in Corey et al (Sci Adv 2021), the dataset which we used to identify the CDL site in GlpG. So essentially, our broader perspective is that we test the common features observed in native proteins in an artificial system. While it is not clear how a peripheral membrane protein like Drp1 fits into this framework, the CDL binding sites in ANTs indeed have the same hallmarks as the one in GlpG (Hedger et al, Biochemistry 2016). We recently contributed to a study demonstrating that the tertiary structure of ANT Aac2 is stabilized by co-purified CDL molecules, underscoring the general validity of our findings (Senoo et al, EMBO J 2024).  We have added this information to the discussion, pg 12, third paragraph, and added a figure (S8, see below) to highlight the architecture of the Aac2-CDL complex.

Overall, using both model and native protein systems, this study convincingly underscores the molecular and structural requirements for CDL binding and binding-induced membrane protein stability. This work provides much-needed insight into the poorly understood nature of protein-CDL interactions.

We thank the reviewer for the positive assessment!

Reviewer #2 (Public review):

Summary:

The work in this paper discusses the use of CG-MD simulations and nMS to describe cardiolipin binding sites in a synthetically designed, that can be extrapolated to a naturally occurring membrane protein. While the authors acknowledge their work illuminates the challenges in engineering lipid binding they are able to describe some features that highlight residues within GlpG that may be involved in lipid regulation of protease activity, although further study of this site is required to confirm it's role in protein activity.

Comments

Discrepancy between total CDL binding in CG simulations (Fig 1d) and nMS (Fig 2b,c) should be further discussed. Limitations in nMS methodology selecting for tightest bound lipids?

We thank the reviewer for pointing out that this needs to be clarified. We analyze proteins in detergent, which is in itself delipidating, because detergent molecules compete with the lipids for binding to the protein, an effect that can be observed in MS (Bolla et al, Angew Chemie Int. Ed. 2020). Native MS of membrane proteins requires stripping of the surrounding lipid vesicle or detergent micelle in the vacuum region of the mass spectrometer, which is done through gentle thermal activation in the form of high-energy collisions with gas molecules. Detergent molecules and lipids not directly in contact with the protein generally dissociate easier than bound lipids (Laganowsky et al, Nature 2014), however, the even loosely bound lipids can readily dissociate with the detergent, artificially reducing occupancy. The nMS data is therefore likely biased towards lipids bound tightly (e.g. via electrostatic headgroup interactions), however, these are the lipids we are interested in, meaning that the use of MS is suitable here. We have noted this in the Discussion, last paragraph on page 12.

Mutation of helical residues to alanine not only results in loss of lipid binding residues but may also impact overall helix flexibility, is this observed by the authors in CG-MD simulations? Change in helix overall RMSD throughout simulation? The figures shown in Fig.1H show what appear to be quite significant differences in APO protein arrangement between ROCKET and ROCKET AAXWA.

For most of the study, we use CG with fixed backbone bead properties as well as an elastic network to maintain tertiary structure. This means that a mutation to alanine will have essentially no impact on the stability of the helix or protein in general in the CG simulations in the bilayer. It should be noted that Figure 1H shows snapshots from atomistic gas phase simulations with pulling force applied (see schematic in Figure 1F, as well as Figure S1 for ends-point structures), where we naturally expect large structural changes due to unfolding. We have analyzed the helix content in the gas-phase simulations and see that helix 1 in ROCKET unwinds within 10 ns but stays helical ca. 10 ns longer when bound to CDL. The AAWXA mutation stabilizes the helical conformation independently of CDL binding, but CDL tethers the folded helix closer to the core (see Figure 1 G and H). We have added this information to the results section and the plot below to Figure S2.

CG-MD force experiments could be corroborated experimentally with magnetic tweezer unfolding assays as has been performed for the unfolding of artificial protein TMHC2. Alternatively this work could benefit to referencing Wang et al 2019 "On the Interpretation of Force-Induced Unfolding Studies of Membrane Proteins Using Fast Simulations" to support MD vs experimental values.

We apologize for the confusion here. The force experiments are gas-phase all-atom MD. The simulations show that the protein-lipid complex has a more stable tertiary structure in the gas phase. Since these are gas-phase simulations, they cannot be corroborated using in-solution measurements. Similarly, the paper by Wang et al is a great reference for solution simulations, however, to date the only validations for gas-phase unfolding come from native MS.

Did the authors investigate if ROCKET or ROCKETAAXWA copurifies with endogenous lipids? Membrane proteins with stabilising CDL often copurify in detergent and can be detected by MS without the addition of CDL to the detergent solution. Differences in retention of endogenous lipid may also indicate differences in stability between the proteins and is worth investigation.

We have investigated the co-purification of the ROCKET variants and did not observe any co-purified lipids (see Figure S4) which we clarified in the results section (page 5, third paragraph) now. We previously showed that long residence times in CG-MD are linked to the observation of co-purified lipids, because they are not easily outcompeted by the detergent (Bolla et al, Angew Chemie Int. Ed. 2020). In CG-MD of ROCKET, we see that although the CDL sites are nearly constantly occupied, the CDL molecules are in rapid exchange with free CDL from the bulk membrane. For MS, all ROCKET proteins were extracted from the E. coli membrane fraction with DDM, which likely outcompetes CDL. This interpretation would explain why we see significant CDL retention when the protein is released from liposomes, but not when the protein is first extracted into detergent. For GlpG, CDL residence times in CG-MD  are longer, which agrees with CDL co-purification. Similarly, there is clearly an enrichment of CDL when the protein is extracted into nanodiscs (Sawczyc et al, Nature Commun 2024).

Do the AAXWA and ROCKET have significantly similar intensities from nMS? The AAXWA appears to show slightly lower intensities than the ROCKET.

We did not observe a significant difference, however, in most spectra, the AAXWA peaks have a lower intensity than those of the other variants (see e.g. Figure S5). While this could be batch-to-batch variations, there may be a small contribution from the lower number of basic residues (see Abramsson et al, JACS au 2021). However, there is an excess of basic residues in the soluble domain of ROCKET, so this interpretation is speculative.

Can the authors extend their comments on why densities are observed only around site 2 in the cryo-em structures when site 1 is the apparent preferential site for ROCKET.

We base the lipid preference of Site 1 > Site 2 on the CG MD data, where we see a higher occupancy for site 1. At the same time, as noted in the text, CDL at both sites have rather short residence times. When the protein is solubilized in detergent, these times can change, and lipids in less accessible sites (such as cavities and subunit interfaces) may be subject to a slower exchange than those that are fully exposed to the micelle (Bolla et al, Angew Chemie Int. Ed. 2020). We speculate that this effect may favor retaining a lipid at site 2. Furthermore, site 1 is flexible, with CDL attaching in various angles while site 2 has more uniform CDL orientations (see CDL density plot in Figure 1D). EM is likely biased towards the less flexible site. Notably, the density is still poorly defined, so it is possible that a more variable lipid position in site 1 would not yield a notable density at all. We have added this information to the Results section (page 5, second paragraph).

The authors state that nMS is consistent with CDL binding preferentially to Site 1 in ROCKET and preferentially to Site 2 in the ROCKET AAXWA variant, yet it unclear from the text exactly how these experiments demonstrate this.

As outlined in the previous answer, we base our assessment of the sites on the CG MD simulations. There, we note that CDL binds predominantly to site 1 in ROCKET and predominantly to site 2 in AAXWA, however, the overall occupancy is lower in AAXWA than in Rocket, meaning fewer lipids will be bound simultaneously in that variant. The nMS data show CDL retention by both variants when released from liposomes, but the AAXWA has lower-intensity CDL adduct peaks (Figure 2B, C). We interpret this that both have CDL sites, but in the AAXWA variant, the sites have lower occupancy. We agree that this observation does not demonstrate that the CG MD data are correct, however, it is the outcome one expects based on the simulations, so we described it as “consistent with the simulations”. We have rephrased the section to make this clear.

As carried out for ROCKET AAXWA the total CDL binding to A61P and R66A would add to supporting information of characterisation of lipid stabilising mutations.

We considered this possibility too. Unfortunately, the mass differences between A61P / R66A and AAXWA are slightly too high to unambiguously resolve CDL adducts of each variant, as the 1st CDL peak of AAWXA partially overlaps with the apo peak of A61P or R66A.

Did the authors investigate a double mutation to Site 2 (e.g. R66A + M16A)?

While designing mutants, we tested several double mutants involving the basic residues that bind the CDL headgroups (e.g. R66 + AAWXA) but found that they could not be purified, probably because a minimum of positive residues at the N-terminus is required for proper membrane insertion and folding. M16 is an interesting suggestion, but wasn’t considered because the more subtle effects of non-charged amino acids on CDL binding may be lost during desolvation (see also our response to Comment (i) from reviewer 1).

Was the stability of R66A ever compared to the WT or only to AAXWA?

Some of the ROCKET mutants have very similar masses that cannot be resolved well enough on the ToF instrument. While the R66-WT comparison is possible, we would not be able to compare it to R61P or D7A/S8R. To avoid three-point comparisons, we selected AAXWA as the common point of reference for all variants.

How many CDL sites in the database used are structurally verified?

At the time, 1KQF was the only verified E. coli protein with a CDL resolved in a high-resolution structure. The complex was predicted accurately, see Figure 6A in Corey et al (Sci Adv 2021), as were several non-E. coli complexes.

The work on GlpG could benefit from mutagenesis or discussion of mutagenesis to this site. The Y160F mutation has already been shown to have little impact on stability or activity (Baker and Urban Nat Chem Biol. 2012).

We thank the referee for their excellent suggestion. While Y160F did not have a pronounced effect, the other 3 positions of the predicted CDL binding site in GlpG have not been covered by Baker and Urban. Looking at sequence conservation in GlpG orthologs, manually sampling down to 50% identity (~1300 sequences in Uniprot) shows that Y160 and K167 are conserved, R92 varies between K/R/Q, whereas W98 is not conserved. The other (weak) site cited above (K132 and K191) is not conserved. A detailed investigation of how the conserved residues impact CDL binding and activity is already planned for a follow up study focusing on GlpG biology.

Reviewer #3 (Public review):

Summary:

The relationships of proteins and lipids: it's complicated. This paper illustrates how cardiolipins can stabilize membrane protein subunits - and not surprisingly, positively charged residues play an important role here. But more and stronger binding of such structural lipids does not necessarily translate to stabilization of oligomeric states, since many proteins have alternative binding sites for lipids which may be intra- rather than intermolecular. Mutations which abolish primary binding sites can cause redistribution to (weaker) secondary sites which nevertheless stabilize interactions between subunits. This may be at first sight counterintuitive but actually matches expectations from structural data and MD modelling. An analogous cardiolipin binding site between subunits is found in E.coli tetrameric GlpG, with cardiolipin (thermally) stabilizing the protein against aggregation.

“It’s complicated” We could not have phrased the main conclusions of our study better.

Strengths:

The use of the artificial scaffold allows testing of hypothesis about the different roles of cardiolipin binding. It reveals effects which are at first sight counterintuitive and are explained by the existence of a weaker, secondary binding site which unlike the primary one allows easy lipid-mediated interaction between two subunits of the protein. Introducing different mutations either changes the balance between primary and secondary binding sites or introduced a kink in a helix - thus affecting subunit interactions which are experimentally verified by native mass spectrometry.

Weaknesses:

The artificial scaffold is not necessarily reflecting the conformational dynamics and local flexibility of real, functional membrane proteins. The example of GlpG, while also showing interesting cardiolipin dependency, illustrates the case of a binding site across helices further but does not add much to the main story. It should be evident that structural lipids can be stabilizing in more than one way depending on how they bind, leading to different and possibly opposite functional outcomes.

We share the reviewer’s concern, as we clearly observe that TMHC4_R does not have the same type of flexibility as a natural protein. We find that by introducing flexibility, we start to see CDL-mediated effects. To test the valIdity of our findings from the artificial system, we apply them to GlpG. In response to a suggestion from Reviewer 1, we compared the findings to Aac2, and found that its stabilizing CDL site closely resembles that in GlpG (see new Figure S8).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Minor comments:

There are a number of typos/uncorrected statements in the text.

i) The last sentence of the Abstract appears to be an uncorrected mishmash of two.

ii) Line 66: "protects" should be just "protect"

iii) Line 75: Sentence appears to be incomplete. "...associated changes in protein stability." The word "stability" is missing.

We have made these changes.

iv) Fig. 2E. Are the magenta and blue colors inverted for variants 1 and 2?

No, the color is correct. greater stabilization of the blue tetramer (AAXAW) compared to WT (purple) will lead to fewer blue monomoers than purple monomers in the mass spectrum.

v) Line 274: the salt bridge should be between R8-E68.

We have corrected this.

vi) Lines 350-354 (final sentence of the paragraph): The sentence does not read well (especially with the double negative element). Please reconstruct the sentence and/or break it into two. 

We have split the sentence in two.

Suggestions:

(i) While aromatic residues (in particular Trp) appear to be clearly involved in the CDL interaction, there is no investigation of their roles and contributions relative to the positively charged residues (R and K) investigated here. How do aromatics contribute to CDL binding and protein stability, and are they differential in nature (W vs Y vs F)?

See our response to comment (i) from reviewer 1. In short, subtle contribution to lipid interactions (such as pi stacking with Trp or Tyr) will likely be lost during transfer to the gas phase. However, see also our response to the last comment from reviewer 2, we plan to use solution-phase activity assays to investigate the effect of Trp on CDL binding to Glp. However, this is beyond thes cope oif the current study.

(ii) In the case of GlpG, a WR pair (W136-R137) present at the lipid-water on the periplasmic face (adjacent to helices 2/3) may function akin to the W12-R13 of ROCKET in specifically binding CDL. Investigation of this site might prove to be interesting if it indeed does.

We added the CDL density plot for the periplasmic side to Figure S7 and discuss further sites in GlpG in the Discussion section. See response to point (ii) above for details.

Reviewer #2 (Recommendations for the authors):

Minor comments

- Typo in abstract line 39-40

- Typo in figure legend of Fig 1 line 145

- Typo in line 149, missing R66 in residues shown as sticks description

- Lines 165-167 could benefit from describing what residues are represented as sticks

We have made these changes.

- Line 263 should refer to the figure where the tetrameric state was not affected by this mutation.

The full spectrum of the A61P mutant is not included in the figure, hence there is no reference,

- Addition of statistics to Fig. 4F ?

We have added significance indicators to the graph and information about the statistics to the legend.

Reviewer #3 (Recommendations for the authors):

Minor issues

l39: rewrite

We have made these changes.

l60: provide evidence for what is presented as a general statement - cardiolipins might also regulate function without affecting oligomeric state, e.g. MgtA

This is a good point, we have added references to two examples where CDL work without affecting oligomerization (MtgA, Weikum et al BBA 2024, and Aac2, Senoo et al, EMBO J 2024).

l74: not every functional interaction comes with a thermal shift

We use thermal shift as a proxy because it indicates tight interactions, even if they may not be functional. We have made this distinction clearer in the text.

l78: this is true for electrostatic interactions such as are at play here, but not necessarily for hydrophobic ones

l133: in what direction is the pulling force applied - the figure seems to suggest diagonally?

The pull coordinate is defined as the distance between the centers of mass of the two helices. The direction of the pull coordinate in Cartesian coordinate space is thus not fixed.

fig 1f, l159: "dissociating" meaning separation of subunits? the placement of the lipid within one subunit would not suggest that intermolecular interactions are properly represented here, please clarify

The lipid placement in the schematic is not representative since the lipid occupies different spaces in WT and AAXWA, we have noted this in the legend. Regarding line 159, “Dissociation” is not strictly correct, since the measure the force to separate helix 1 and 2, i.e. unfolding. We have changed the wording to “unfolding”.

l173: was there any evidence in EM data for monomers or smaller oligomers?

No smaller particles were identified by visual inspection or in the particle classes. We have noted this in the methods section.

l203: were tetramer peaks isolated separately for CID?

C8E4 can cause some activation-dependent charge reduction, which could allow some tetramers to “sneak out” of the isolation window. We used global activation without precursor selection which subjects all ions to activation.

fig 2c: can you indicate the 3rd lipid binding as it seems to be in the noise

We can unambiguously assign the retention of three CDL molecules for 17+ charge state only, and clarified this in the legend to Figrue 2.

fig3: can you pls clarify what is meant by stabilization here - less monomer in case A means a more stable oligomer, but "A > B" should lead to ratios < 50%. This does not help with understanding what "stabilization" means in panels c-f, please define what the y axis means for these. Please also explain the bottom panels (side view) in each case, what do the dots represent?

We apologize for the oversight of not explaining the side views, we have added a legend. The schematic in panel A is correct (compare the schematic in Figure 2 E). If tetramer A (blue) is stabilized by CDL more than tetramer B  “CDL stabilization A>B”), there will be fewer monomers ejected from A. If there is less A in the presence of CDL, then the ratio of B/(B+A) will go up.

It is not very clear what consequences the kink introduced by proline has for intra- vs. intermolecular interactions - the cartoons don't help much here

We agree, the A61P impact on the structure is subtle. The small kink it introduces is not really visible in the top view, and hence, we tried to emphasize this in the side view. We have clarified the meaning of the side view schematics in the legend.

l360: is that an assumption made here or is there evidence for displacement? native MS could potentially prove this.

This is an assumption based on the fact that we see very little binding of POPG in the mixed bilayer CG-MD. We have clarified this in the text. Measuring this with MS is an interesting idea, but we have no direct measurement of displacement, since addition of CDL and POPG to the protein in detergent would result in binding to other sites as well.

fig 4d: there is not much POPG density visible at all - why is that?

Both plots use the same absolute scale. There is simply much less POPG binding compared to CDL.

fig 4e: is this released protein already dissociated into monomers due to denaturation or excessive energy (CID product) - please comment.

The CID energy for the spectrum in Figure 4E was selected to show partial dissociation and monomer release at higher voltages (220V in this case). At lower voltages (150V-170V) we do not observe dissociation in C8E4, see Figure S4A.

l363: pls comment on the apparent discrepancy between single lipid binding and double density

We added a clarifying sentence regarding the double lipids. The density seen in the published structure is of four lipid tails next to each other, which is what one would expect for a CDL. Since the CDL could not be resolved unambiguously, two phospholipids with two acyl chains each were modeled into the density instead. Our MS and MD data strongly suggests that the density stems from a single CDL.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Fernandez et al. investigate the influence of maternal behavior on bat pup vocal development in Saccopteryx bilineata, a species known to exhibit vocal production learning. The authors performed detailed longitudinal observations of wild mother-pup interactions to ask whether non-vocal maternal displays during juvenile vocal practice or 'babbling', affect vocal production. Specifically, the study examines the durations of pup babbling events and the developmental babbling phase, in relation to the amount of female display behavior, as well as pup age and the number of nearby singing adult males. Furthermore, the authors examine pup vocal repertoire size and maturation in relation to the number of maternal displays encountered during babbling. Statistical models identify female display behavior as a predictor of i) babbling bout duration, ii) the length of the babbling phase, iii) song composition, and iv) syllable maturation. Notably, these outcomes were not influenced by the number of nearby adult males (the pups' source of song models) and were largely independent of general maturation (pup age). These findings highlight the impact of non-vocal aspects of social interactions in guiding mammalian vocal development.

We thank Reviewer 1 for the time and effort dedicated to the revision of our study. The suggestions for the revision of our manuscript were very helpful and have improved our manuscript considerably. 

Strengths:

Historically, work on developmental vocal learning has focused on how juvenile vocalizations are influenced by the sounds produced by nearby adults (often males). In contrast, this study takes the novel approach of examining juvenile vocal ontogeny in relation to non-vocal maternal behavior, in one of the few mammals known to exhibit vocal production learning. The authors collected an impressive dataset from multiple wild bat colonies in two Central American countries. This includes longitudinal acoustic recordings and behavioral monitoring of individual mother-pup pairs, across development.

The identified relationships between maternal behavior and bat pup vocalizations have intriguing implications for understanding the mechanisms that enable vocal production learning in mammals, including human speech acquisition. As such, these findings are likely to be relevant to a broad audience interested in the evolution and development of social behavior as well as sensory-motor learning.

We thank reviewer 1 for this assessment. 

Weaknesses:

The authors qualitatively describe specific patterns of female displays during pup babbling, however, subsequent quantitative analyses are based on two aggregate measures of female behavior that pool across display types. Consequently, it remains unclear how certain maternal behaviors might differentially influence pup vocalizations (e.g. through specific feedback contingencies or more general modulation of pup behavioral states).

In analyzing the effects of maternal behavior on song maturation, the authors focus on the most common syllable type produced across pups. This approach is justified based on the syllable variability within and across individuals, however, additional quantification and visual presentation of categorized syllable data would improve clarity and potentially strengthen resulting claims.

We agree that our analysis of maternal behaviour does not investigate potential contingencies between particular maternal behavioural displays and pup vocalizations (e.g. particular syllable types). Our data collected for this study on maternal behaviour includes direct observations, field notes and/or video recordings. In the future, it will be necessary to work with high-speed cameras for the analysis of potential contingencies between particular maternal behavioural displays and specific pup vocalizations, which allow this kind of fine-detailed analysis. We have planned future studies investigating whether pup vocalizations elicit contingent maternal responses or vice versa. In the revision of our manuscript, we have included a comment pointing out that this special behaviour will be investigated in greater detail in the future. 

As suggested by reviewer 1, in our revised manuscript we have included more information on methods to improve understandability. In particular, we have:

-presented more information on different steps of our acoustic analyses

-provided additional and clearer spectrogram figures representing the different syllable types and categorizations 

-changed the figures accompanying our GLMM analyses following the suggestion of Reviewer 1

Reviewer #2 (Public review):

Summary:

This study explores how maternal behaviors influence vocal learning in the greater sac-winged bat (Saccopteryx bilineata). Over two field seasons, researchers tracked 19 bat pups from six wild colonies, examining vocal development aspects such as vocal practice duration, syllable repertoire size, and song syllable acquisition. The findings show that maternal behaviors significantly impact the length of daily babbling sessions and the overall babbling phase, while the presence of adult male tutors does not.

The researchers conducted detailed acoustic analyses, categorizing syllables and evaluating the variety and presence of learned song syllables. They discovered that maternal interactions enhance both the number and diversity of learned syllables and the production of mature syllables in the pups' vocalizations. A notable correlation was found between the extent of acoustic changes in the most common learned syllable type and maternal activity, highlighting the key role of maternal feedback in shaping pups' vocal development.

In summary, this study emphasizes the crucial role of maternal social feedback in the vocal development of S. bilineata. Maternal behaviors not only increase vocal practice but also aid in acquiring and refining a complex vocal repertoire. These insights enhance our understanding of social interactions in mammalian vocal learning and draw interesting parallels between bat and human vocal development.

We thank reviewer 2 for his/her time and effort dedicated to the revision of our study. The suggestions were very helpful in improving our manuscript. 

Strengths:

This paper makes significant contributions to the field of vocal learning by looking at the role of maternal behaviors in shaping the vocal learning phenotype of Saccopteryx bilineata. The paper uses a longitudinal approach, tracking the vocal ontogeny of bat pups from birth to weaning across six colonies and two field seasons, allowing the authors to assess how maternal interactions influence various aspects of vocal practice and learning, providing strong empirical evidence for the critical role of social feedback in non-human mammalian vocal learners. This kind of evidence highlights the complexity of the vocal learning phenotype and shows that it goes beyond the right auditory experience and having the right circuitry.

The paper offers a nuanced understanding of how specific maternal behaviors impact the acquisition and refinement of the vocal repertoire, while showing the number of male tutors - the source of adult song - did not have much of an effect. The correlation between maternal activity and acoustic changes in learned syllable types is a novel finding that underscores the importance of non-vocal social interactions in vocal learning. In vocal learning research, with some notable exceptions, experience is often understood as auditory experience. This paper highlights how, even though that is one important piece of the puzzle, other kinds of experience directly affect the development of vocal behavior. This is of particular importance in the case of a mammalian species such as Saccopteryx bilineata, as this kind of result is perhaps more often associated with avian species.

Moreover, the study's findings have broader implications for our understanding of vocal learning across species. By drawing parallels between bat and human vocal development (and in some ways to bird vocal development), the paper highlights common mechanisms that may underlie vocal practice and learning in both humans and other mammals. This interdisciplinary perspective enriches the field and encourages further comparative studies, ultimately advancing our knowledge of the evolutionary and developmental processes that shape vocal productive learning in all its dimensions.

We thank reviewer 2 for this assessment. 

Weaknesses:

Some weaknesses can be pointed out, but in fairness, the authors acknowledge them in one way or another. As such, these are not flaws per se, but gaps that can be filled with further research.

Experimental manipulations, such as controlled playback experiments or controlled environments, could strengthen the causal claims by directly testing the effects of specific maternal behaviors on vocal development. Certainly, the strengths of the paper will be consolidated after such work is performed.

The reliance on the number of singing males as a proxy for social acoustic input. This measure does not account for the variability in the quality, frequency, or duration of the male songs to which the pups are exposed. A more detailed analysis of the acoustic environment, including direct measurements of song exposure and its impact on vocal learning, would provide a clearer understanding of the role of male tutors.

Finally, and although it would be unlikely that these results are unique to Saccopteryx bilineata, the study's focus on a single species limits at present the generalizability of some of its findings to other vocal learning mammals. While the parallels drawn between bat and human vocal development are intriguing, the conclusions will be more robust when supported by comparative studies involving multiple species of vocal learners. This will help to identify whether the observed maternal influences on vocal development reported here are unique to Saccopteryx bilineata or represent a broader phenomenon in chiropteran, mammalian, or general vocal learning. Expanding the scope of research to include a wider range of species and incorporating cross-species comparisons will significantly enhance the contribution of this study to the field of vocal learning.

Thank you for your suggestions and comments. 

Regarding your main comment 1: In the future, we plan to implement temporary captivity experiments to investigate how maternal behaviours affect pup vocal development. This study provides the necessary basis for conducting future playback studies investigating specific behaviours in a controlled environment.

Regarding your main comment 2: We completely agree that the number of singing males only represents a proxy for acoustic input that pups receive during ontogeny. In the future, we plan to investigate in detail how the acoustic landscape influences pup vocal development and learning. This will include quantifying how long pups are exposed to song during ontogeny and assessing the influence of different tutors, including a detailed analysis of song syllables of the adult tutors to compare it to vocal trajectories of song syllables in pups. 

Regarding your main comment 3: We also fully agree that it is unlikely that these results are unique to Saccopteryx bilineata. We are certain that other mammalian vocal learners show parallels to the vocal development and learning processes of S. bilineata. Especially bats are a promising taxon for comparative studies because their vocal production and perception systems are highly sophisticated (due to their ability to echolocate). The high sociability of this taxon also includes a variety of social systems and vocal capacities (e.g. regarding vocal repertoire size, vocal learning capacities, information content, etc.) which support social learning and social feedback – as shown in our study. 

As suggested, in our revised manuscript we have includes information on the validation of the ethogram. Furthermore, we have corrected all the spelling mistakes – thank you very much for pointing them out!

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

The following comments and suggestions are offered to improve clarity and strengthen support for the paper's main claims.

(1) Female displays as feedback:

a) The authors rather broadly describe maternal behavior as feedback based on its occurrence during pup babbling. Feedback typically entails some degree of response contingency, which is not explicitly established here. Although the authors qualitatively describe a variety of female displays that only occur within the babbling context, they also state that "all these behaviors could occur singly or in an interactive way" (Line 102). The authors go on to use aggregate counts of these diverse female displays in their analyses. It would of course be interesting to know whether distinct female displays are evoked differentially by pup behavior and whether specific female behaviors, in turn, predict subsequent pup vocalizations. A display-specific approach might also reveal more about the mechanisms by which the female behavior shapes babbling (e.g. specific reinforcement signals vs. more graded social facilitation or 'audience effect'). However, even without identifying such finegrained contingencies, the main text should at least mention the results shown in Figure 1A. Namely, that pups initiate ~80% of interactive behavioral sequences, suggesting that subsequent maternal displays are likely to be pup-contingent responses (i.e. feedback) and not simply co-occurring behavior.

We fully agree with Reviewer 1 that it would be very informative to investigate whether distinct female displays are evoked differentially by pup behavior, such as specific syllables within babbling. Or conversely, whether specific female behaviors precede particular pup vocalizations. For this study, we documented maternal behavior through direct observations, field notes, and/or video recordings. However, to capture potential contingencies between specific maternal behavioral displays and vocalization occurring in the millisecond range, other data collection methods (e.g. high-speed camera) will be required in the future. 

Related to this, we have included the following statements (see below). Statement 1 also cites a very recent study in zebra finches, demonstrating that female calls can promote song learning success (Bistere et al. 2024, line 57, lines 304-305). 

Lines 297-305: This finding serves as an initial indication that non-vocal interactions with the mother may influence a pup´s individual learning trajectories. Future studies will focus on the relationship between acoustic change, maternal feedback, and learning success, specifically investigating contingencies between particular pup vocalizations and maternal displays in natural settings. Playback experiments are an additional approach to test the impact of contingency on vocal learning. For example, one study in zebra finches demonstrated that contingent non-vocal maternal feedback affects imitation success (Carouso-Peck & Goldstein, 2019), while another recent study found that female calls can promote song learning but the role of contingency remains to be determined (Bistere et al., 2024).  

Lines: 332-334: This might also apply to S. bilineata where pups initiated ~ 80% of social interactions, suggesting that maternal feedback is likely influenced by the pup´s vocal practice.  

b) The authors claim that the number of maternal displays during babbling predicts the duration of babbling bouts (Figure 1D). I find this analysis - and others based on the raw number of behaviors during babbling - difficult to interpret given that the raw number of displays may depend upon the duration of the babbling bout over which they are counted. In other words, might the number of displays reflect the fact that more displays can occur within the interval of longer babbling bouts? It would be relatively straightforward to minimize this potential confound by testing whether female display *rates* predict longer bouts.

We calculated the display rates (maternal displays per bout duration) and conducted a GLMM (the same analysis after log-transformation and scaling) like in our original manuscript (model 1).  

GLMM

summary(vocpracf)

Generalized linear mixed model fit by maximum likelihood (Laplace Approximation) ['glmerMod']  Family: Gamma  ( log )

Formula: bout_dur ~ age.z + behavioural_quotient.log.z + nomales.z + (1 | ID) Data: set1

Author response table 1.

Author response table 2.

Author response table 3.

Author response table 4.

Author response table 5.

Interpretation: Our analysis in the original manuscript shows that the bout duration increases with number of maternal displays. As reviewer 1 points out: more time offers more opportunities for the mother to show displays. The number of displays in longer bouts could just reflect that more displays are possible in a longer period. This could be a potential confounding factor. However, our analysis of display rates as an explaining factor shows that the relationship between bout duration and display rate is negative. This means that in longer bouts the displays increase (as seen in the first scenario), but they happen less frequently per time unit. This could indicate that in longer bouts, the mother takes breaks or longer periods of time between each display, which decreases the frequency of displays. This minimizes the risk of a potential confound, as it shows that the rate of displays tends to decrease rather than increase in longer bouts. In summary: The display rate does not appear to ‘favour’ longer bouts, as longer bouts are associated with a lower display rate. This speaks against the hypothesis that the number of displays only increases due to the longer bout duration. This also means that our analyses, which show that maternal displays influence song syllable production, are not biased or confounded by the bout duration. This suggests that maternal behaviour is targeted and selective, and represents a potentially contingent reaction to the pup´s vocal production, and is not simply determined by the duration of a bout.

We added this analysis in our supplementary material (Table S2) and pointed this out in the revision of our main manuscript (lines 136-138). 

c) The introduction states that "Pup babbling is not tied to a specific function." (Lines 75-78). This may be an important point worth exploring with this unique data set. For example, the termination of a babbling bout is defined in some cases by the onset of nursing. Have the authors (or others) tested whether babbling elicits nursing behavior? If so, this may represent a reinforcement mechanism that affects babbling rates and subsequent song outcomes. Similar functional shifts in developing vocal behavior have been reported in male chipping sparrows, in which juvenile begging calls - which initially elicit parental feeding behavior - can later be incorporated into 'sub-song' (i.e. babbling) during the development of courtship song (Lui, Wada, Nottebohm, PLOS ONE, 2009).

Thank you for pointing out this interesting study on chipping sparrows! 

To address your question: Strauss et al. (2010) conducted a study on pup and maternal behaviors, demonstrating that babbling did not consistently result in nursing.  When denied care, pups often returned to resting or grooming, a pattern we also observed in our study. While nursing might provide an additional reinforcement mechanisms, it is not the cause that evokes babbling – this is what we mean by stating “pup babbling is not tied to a specific function”. Babbling is not a begging behavior as described by Lui et al. 2009. As mentioned in the review of ter Haar et al. 2021, babbling differs structurally from begging in that it is composed of both adult-like and juvenile syllables and lacks context specificity. To solicit care (i.e. begging) pups produce several isolation calls in a fast repetitive manner. We added a more detailed explanation to make this distinction clear (lines 79-83).

Another interesting fact and probably more comparable to the study of the chipping sparrows – in which begging calls are incorporated into subsong practice – might be the isolation call syllables of S. bilineata. Directly after birth, S. bilineata pups produce multisyllabic isolation calls (see Knörnschild & von Helversen 2008, Knörnschild et al. 2012, Fernandez & Knörnschild 2017) that serve to solicit maternal care. For the first 2.5 weeks, pups only produce innate vocalizations, including echolocation and isolation calls (Fernandez et al. 2021). During the babbling phase, the syllables encoding the individual (and group) signature of the isolation call are also incorporated into babbling bouts. The production of isolation calls might also mark an initial step in the vocal learning process. However, in contrast to the subsong of chipping sparrows, babbling bouts in S. bilineata also include syllables acquired through vocal imitation. Thus, although we find similarities in vocal practice and development between chipping sparrows and S. bilineata, there are also distinct differences. 

(2) Are pups exposed to more male songs when the mother is present?

The number of singing males in each colony was used as a reasonable proxy for the amount of social acoustic input. However, I wonder if pups are exposed to more adult male songs when the mother is present and, relatedly, if females tend to remain present for longer if a pup is babbling (potentially increasing its exposure to male songs during the babbling phase).

The mother is always present when males are singing. In S. bilineata, males predominantly engage in territorial song twice daily: at dusk and dawn. After foraging at night, territorial singing males are the first to return to the roost, and females will only return when they hear male song. Pups are either attached to the mother´s belly or – when growing older – will fly into the roost followed by the mother. In the evening, males sing approximately half an hour before leaving for foraging. Females will usually leave first, followed by their pups, and males leave last. Hence, females/mothers are always present when pups are exposed to male acoustic input.  

(3) Pup sex differences:

The authors test for sex differences within a subset of pups and briefly mention that vocal development is considered in both males and females. This presumably means that female pups also exhibit vocal imitation of adult male territorial songs, even though they only produce these vocalizations during the babbling phase, after which they stop singing entirely. If so, this would, to my knowledge, be a unique phenomenon among vocal learners and would be interesting to discuss in greater detail.

We followed your recommendation and discussed this topic in greater detail. We included the following part in our discussion (lines 257-269): An intriguing aspect of this species is that, unlike most song-learning songbird species, female pups show no differences from males in babbling behavior and vocal development (Fernandez et al. 2021). This study corroborated this finding: female pups received the same maternal feedback, and their song syllable imitation did not differ in any way from male pups (as observed as well in Knörnschild et al. 2010). This phenomenon is rare among vocal learners and raises the question of why female pups match male vocal development despite not using the learned vocalizations later in life. One potential explanation might lie in the function of the territorial song for adult females: it serves as an acoustic signal to help females locate new suitable colonies after dispersal. The territorial song exhibits different dialects, with females showing a preference for local over foreign dialects (Knörnschild et al., 2017). The own early practice and production of song might enhance the ability to evaluate male song and support mating decisions.

(4) Characterization of song syllables:

The authors explain their acoustic analyses in detail within the methods, however, descriptions of the syllable classification procedures and acoustic movement analyses need to be presented more clearly in the main text, so readers unfamiliar with bioacoustics or previous work can follow the logic. Also, given the qualitative descriptions of the data and the two spectrogram examples provided (Figures 2 and S1), it is difficult for the reader to fully evaluate the suitability and output of these critical procedures.

Suggestions:  

- Qualitative descriptions of syllable characteristics (i.e. buzz, pulse, trill, ripple, gap, smeared noisy, precursor syllable, mature syllable, adult-like syllable, early vs. late babbling phase, syllable name, etc) should all be clearly-labeled in example spectrograms and used consistently, without using different terms interchangeably (e.g. mature vs. adult-like).

We understand that we should provide a clearer description of the various terms essential to understanding this study. We added a “Terminology” box (line 158) to the main manuscript, defining the acoustic terms we are using throughout our study. Additionally, we enhanced Figure S1 by providing more detailed information on the spectrogram that displays the five distinct song syllable types. Moreover, we included an additional spectrogram in the supplementary material (Fig. S2) displaying examples of precursor and mature syllables for syllable B2. In the method section, “The acoustic movement during ontogeny”, we added a sentence clarifying the terms “early” and “late babbling phase” (Lines 605-606). 

- Show as you tell. Plot the data, at least from a representative pup, for each major step in the analyses (labeled spectrogram, PCA plots with distinct syllable clusters, high vs. low versatility, precursor vs. mature variants, early vs. late syllables with Euclidean distances between centroids and relation to "generic" adult male syllables, etc.)

To illustrate the acoustic analysis more comprehensively, we have made the following additions:

-we included a Figure (Fig. S3) in the supplementary materials showing an excerpt of a babbling bout with labelled syllables to illustrate how we analyzed a) total song syllable count per bout, b) versatility per bout, and c) the number of precursor versus mature B2 syllables (the most common syllable type).

-Additionally, we included a spectrogram with three exemplary B2 syllables to illustrate the acoustic parameter extraction with Avisoft SASLab Pro software for subsequent analysis of vocal change during development (Fig. S4 A).

Lastly, we included a DFA for one of the colonies with three exemplary pups to illustrate how we calculated each pup's acoustic change during ontogeny (Fig. S4 B). 

(5) Minor Comments and Corrections:

- Modeled data are log-transformed, however, the raw data are plotted on linear scales, and in most cases, data points are densely clustered and overlapping at lower values. Plotting the data on log scales would likely aid visibility.

We appreciate this suggestion and changed the plots accordingly. 

- Figure 1E displays 18 data points, (legend says n=19).

The legend is correct; the figure includes 19 data points. Two mothers have the same activity score, so their points are at the same location and it looks like there are only 18 data points. 

- Line 482: Is "VCL" media player meant to refer to "VLC" player?

Yes, thank you for spotting that. We corrected it.  

Reviewer #2 (Recommendations for the authors):

I have only a couple of comments:

- Perhaps it would be useful to briefly go over the validation used for the ethogram in Table S1.

The behaviors listed in the ethogram were defined based on Strauss et al. (2010) and expanded based on our own observations. For consistency, we developed these definitions and trained the students analyzing behavioral data for this study. During the training phase, we validated their analyses until the inter-observer-reliability reached 100% (lines 507-508).  

- The paper seems to be generally written in American English, yet there are some instances of British English spelling, e.g. "standardised"/"standardisation": table 1, table 2, lines 143, 228, 524, 525, 531, 546, 547, 554, 560, 561.

Thank you for spotting these errors, we corrected them.  

- Line 343: "at libitum" should be "ad libitum".

Thank you for spotting this error. We corrected it.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:  

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.

We have performed protein blotting and proteomics to characterize ER-FlucDM-eGFP expressing cells. We have also provided evidence to support the role of ER reorganization in regulating aggregate clearance. Our proteomic analysis provided a global view of the cellular state of cells expressing ER-FlucDM-eGFP, which potentially revealed functional relevance of ER-FlucDM-eGFP. Details are explained in the following comments. 

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 ERtargeted 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 singlelayer 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.

We have included a previous study that showed accumulation of BiP aggregates in the nucleus upon overexpression of BiP (Morris et al., 1997; DOI: 10.1074/jbc.272.7.4327) in the discussion (Line 299).

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.

We initially made mStayGold-Sec61β to image the ER structures and ER-FlucDM-eGFP aggregates. However, we could not obtain convincing time-lapse images to show the release of ER-FlucDM-eGFP aggregates from the ER membrane as there are abundant ER structures present close to the aggregates during mitosis, preventing the differentiation of the membrane encapsulating aggregates from the ER structures. 

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?

We performed cycloheximide chase experiments in cells released from the G2/M and found that ER-FlucDM-eGFP protein level did not fluctuate significantly when cells progressed through mitosis and cytokinesis. Thus, we did not consider protein ubiquitination and degradation of ER-FlucDM-eGFP as a major mechanism for its clearance. We have included this observation in the results (Figure S7A; Line 266) and in the discussion (Line 324) of the revised manuscript.

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. 

We performed solubility test in cells expressing ER-FlucDM-eGFP and detected insoluble ERFlucDM-eGFP after heat stress (Figure S1E; Line 102). We have also performed protein blotting to detect ER-FlucDM-eGFP to normalize the luciferase activity (Line 609). We have updated the method section for luciferase measurement (Line 494).   

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.

We performed cycloheximide chase experiments in cells released from the G2/M and found that ER-FlucDM-eGFP protein level did not fluctuate significantly when cells progressed through mitosis and cytokinesis (Figure S7A to S7C). Also, live-cell imaging of cells released from the G2/M indicated no significant change of total fluorescence intensity of ER-FlucDMeGFP (Figure S7D). Thus, we do not think that protein degradation of ER-FlucDM-eGFP is the major mechanism for its clearance. 

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.

We have re-transduced fresh MCF10A cells with lentiviral particles to induce expression of ER-FlucDM-eGFP. The aggregates started to form after 24 h post-transduction. We made similar observations as described in the manuscript (e.g. aggregate clearance) two days after re-transduction.

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.

We have performed proteomic analysis in cells expressing ER-FlucDM-eGFP and observed up-regulation of multiple proteins involved in the ER stress response, indicating that cells expressing ER-FlucDM-eGFP experience proteostatic stress (Figure S4A; Line 179).  

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.

We have co-expressed ER-FlucDM-mCherry and mStayGold-Sec61β and detected mStayGold- Sec61β around ER-FlucDM-mCherry aggregates (Figure 1B).  

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.

We targeted FlucDM-eGFP to the nucleus by expressing NLS-FlucDM-eGFP (Figure S1A). We found that the nuclear FlucDM-eGFP did not co-localize with the ER-FlucDM-mCherry aggregates (Figure S1B; Line 96). We have also determined the expression levels of NLSFlucDM-eGFP and ER-FlucDM-mCherry (Figure S1C and S1D).

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.

Thank you for interesting suggestions for our study. We speculated that ER-FlucDM-eGFP aggregates may derive from the invagination of the inner nuclear membrane given that the aggregates are in close proximity to the inner nuclear membrane in interpase cells (Line 299). We have included a previous study that reported a similar aggregate upon BiP overexpression (Morris et al., 1997; DOI: 10.1074/jbc.272.7.4327; Line 300). Our proteomic analysis showed that cells expressing ER-FlucDM-eGFP have several up-regulated proteins related to cell cycle regulation (Figure S4A; Line 346).  

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.

We have included images to show that BiP co-localizes with ER-FlucDM-eGFP aggregates in interphase cells (Figure S5C). We think that BiP participates in the formation of ER-FlucDMeGFP during interphase instead of getting recruited to the aggregates during mitosis.  

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

We provided evidence to show that clearance of ER-FlucDM-eGFP aggregates involves the ER remodeling process. We depleted ER membrane fusion proteins ATL2 and ATL3 to perturb the distribution of ER sheets or tubules and found that cells were defective in clearing the aggregates (Figure 7A and B; Line 278). 

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

In our proteomic analysis, we found that BiP (HSPA5) but not other Hsp70 family members were up-regulated in cells expressing ER-FlucDM-eGFP (Line 352; Figure S4A). This explains why BiP is the main player of the ER-FlucDM-eGFP aggregate clearance.  

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.

In our revised manuscript, we now provided evidence to show that ER-FlucDM-eGFP aggregate clearance involved remodeling of the ER structures during mitotic exit. This is added as a new Figure 7 in the revised manuscript and is described in the result section (Line 278) and in the discussion section (Line 323). We believe that this addition has provided mechanistic insights into ER-FlucDM-eGFP aggregate clearance.

Recommendations for the authors:

Reviewing Editor comments:

I have read these reviews in detail and would like to recommend that the authors perform the experiments according to the reviewers' suggestions, as well as provide the appropriate controls raised by the reviewers.

I think there are not that many requests and they all seem very reasonable and easily doable. I would recommend that the authors carry out the suggested experiments to develop a stronger story where the evidence transitions from being incomplete presently to a "more complete" standard.

We have addressed questions raised by three reviewers and updated our manuscript (labeled in red in the main text).

Reviewer #1 (Recommendations For The Authors):

The manuscript makes exciting observations about the accumulation of reporter protein aggregates in the nucleus and its clearance during mitosis. It also provides some insight into the role of chaperons in aggregate clearance. These observations provide a good platform to perform in-depth analysis of the underlying mechanism and its functional relevance which perhaps the authors will plan over the long term. However, the below suggestions will help improve the current version of the manuscript:

(1) Although it is assumed that the aggregates are cleared by the protein degradation mechanism, clear evidence supporting this assumption in the author's experiments is lacking and needs to be provided. Is it possible that mitosis induces disassembly of these aggregates instead of degradation?

We performed two experiments to verify whether ER-FlucDM-eGFP aggregates are cleared by the protein degradation mechanism. In the first experiment, we treated cells expressing ER-FlucDM-eGFP released from the G2/M boundary with cycloheximide (CHX) and found that ER-FlucDM-eGFP did not decrease in protein abundance in cells progressing through mitosis (Figure S7A to S7C). In the second experiment, we measured the intensity of ERFlucDM-eGFP in early dividing cells and late dividing cells after release from the G2/M boundary and found that there was no significant difference between early and late dividing cells (Figure S7D). Thus, we concluded that protein degradation of ER-FlucDM-eGFP is not the primary mechanism of its clearance during cell division (Line 324). Furthermore, we included new data to show that the ER-FlucDM-eGFP aggregate clearance depends on ER reorganization during cell division, so mitotic exit induces disassembly of the aggregates instead of protein degradation.

(2) It is intriguing that the aggregates are nuclear. Is the nuclear localization mediated by localization to ER? A time course analysis would reveal this and would provide credence to the idea that the reporter was originally expressed in the ER. It is currently unclear if the reporter ever gets expressed in ER.

We showed that in interphase cells, ER-FlucDM-eGFP co-localizes with mStayGold-Sec61β, which labels the ER structures (Figure 1B). So, ER-FlucDM-eGFP is expressed and present in the ER network and invaginates into the inner nuclear membrane as aggregates. We attempted to image ER-FlucDM-eGFP for its formation; however it was technically challenging as the aggregates appeared very small and not too visible after clearance under our microscopy system.  

(3) It would be expected that the persistence of these aggregates would impact cell division and cellular health. An experiment addressing this hypothesis would be very useful in establishing the functional relevance of this observation in the context of the current study.

We have performed proteomic analysis on cell expressing ER-FlucDM-eGFP and found that multiple proteins involved in the ER stress response were up-regulated (Figure S4A). Additionally, proteins related to cell cycle regulation were up-regulated upon expression of ER-FlucDM-eGFP (Figure S4A). The increase of these proteins may indicate a perturbed cellular health (Line 344). 

(4) A recent report (PMID: 34467852) identified the role of ER tubules in controlling the size of certain misfolded condensates. Would specific ER substructures affect the nuclear localization and/or clearance of the FlucDM aggregates? This is tied to point#2 and would provide insights into the connection between ER and the nuclear aggregates.

Thank you for your suggestions. We perturbed the ER remodeling process by knocking down ATL2 and ATL3, which are ER membrane fusion proteins, and found that clearance of ER-FlucDM-eGFP aggregates was affected (Figure 7A and B). Hence, perturbation of the distribution of ER tubules and ER sheets affects ER-FlucDM-eGFP aggregate clearance. We have also added the recent paper about ER tubule size in regulating the sizes of misfolded condensates in the discussion (Line 321)

Reviewer #2 (Recommendations For The Authors):

I expect that the images indicate z-sections. Should be indicated in legends as applicable.

We have indicated whether the images are Z-stack or single Z-slices in the figure legends.  

Small point: the control region (outside inclusion) that was bleached in 2c may be clearly indicated. 

We have added the explanation in the figure legend of Figure 2C.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

The authors investigate the neuroprotective effect of reserpine in a retinitis pigmentosa (P23H-1) model, characterized by a mutation in the rhodopsin gene. Their results reveal that female rats show better preservation of both rod and cone photoreceptors following reserpine treatment compared to males.

Strengths:

This study effectively highlights the neuroprotective potential of reserpine and underscores the value of drug repositioning as a strategy for accelerating the development of effective treatments. The findings are significant for their clinical implications, particularly in demonstrating sex-specific differences in therapeutic response.

We sincerely appreciate the reviewer’s comments.

Weaknesses:

The main limitation is the lack of precise identification of the specific pathway through which reserpine prevents photoreceptor death.

We acknowledge that the exact pathway through which reserpine exerts its protective effects on photoreceptors remains undetermined, yet our findings provide critical insights into potential mechanisms. Together with our previous report [PMID: 36975211], the studies being presented here validate proteostasis (including autophagy) and p53 signaling as the key pathways underlying reserpine-mediated survival of photoreceptors in retinal disease models. We also go a step further by showing an influence of the biological sex.

We emphasize that the primary aim of this study was to demonstrate the effectiveness of reserpine in a different retinal degeneration model—specifically, the autosomal dominant RP model—which shares a retinal disease phenotype with the model used for initial screening but involves different genetic and molecular mechanisms of degeneration.

Reviewer #2 (Public review):

Summary:

In the manuscript entitled "Sex-specific attenuation of photoreceptor degeneration by reserpine in a rhodopsin P23H rat model of autosomal dominant retinitis pigmentosa" by Beom Song et al., the authors explore the transcriptomic differences between male and female wild-type (WT) and P23H retinas, highlighting significant gene expression variations and sex-specific trends. The study emphasizes the importance of considering biological sex in understanding inherited retinal degeneration and the impact of drug treatments on mutant retinas.

Strengths:

(1) Relevance to Clinical Challenges: The study addresses a critical limitation in inherited retinal degeneration (IRD) therapies by exploring a gene-agnostic approach. It emphasizes sex-specific responses, which aligns with recent NIH mandates on sex as a biological variable.

(2) Multi-dimensional Methodology: Combining electroretinography (ERG), optical coherence tomography (OCT), histology, and transcriptomics strengthens the study's findings.

(3) Novel Insights: The transcriptomic analysis uncovers sex-specific pathways impacted by reserpine, laying the foundation for personalized approaches to retinal disease therapy.

We are grateful for highlighting the strengths of our work.

Weaknesses:

Dose Optimization

The study uses a fixed dose (40 µM), but no dose-response analysis is provided. Sex-specific differences in efficacy might be influenced by suboptimal dosing, particularly considering potential differences in metabolism or drug distribution.

We acknowledge the limitation of using a fixed dose (40 µM) of reserpine in this study without conducting a comprehensive dose-response analysis. In the primary screens, the EC₅₀ of reserpine was approximately 20 µM. We doubled the concentration for injection to account for the potential loss of reserpine during the in vivo procedures. As we observed the rescue effect of reserpine in mice, we used the same concentration for rats. The fixed-dose approach was chosen to maintain consistency with previous studies evaluating reserpine in retinal degeneration models and to facilitate comparison across studies. Efforts to identify optimal dosing were deprioritized, as the primary goal was different and this information cannot be directly translated to clinical applications.

We also agree that sex-specific differences in efficacy might be influenced by suboptimal dosing, particularly given potential variations in metabolism, drug distribution, and pharmacokinetics between male and female rats. However, recent pharmacokinetic studies on systemically administered reserpine in rats reported no statistically significant covariates, including body weight, age, breed, or sex, affecting pharmacokinetic (PK) or pharmacodynamic (PD) parameters (Alfosea-Cuadrado, G. M., Zarzoso-Foj, J., Adell, A., Valverde-Navarro, A. A., González-Soler, E. M., Mangas-Sanjuán, V., & Blasco-Serra, A. (2024). Population Pharmacokinetic–Pharmacodynamic Analysis of a Reserpine-Induced Myalgia Model in Rats. Pharmaceutics, 16(8), 1101. https://doi.org/10.3390/pharmaceutics16081101). Furthermore, no evidence of sex-specific differences in reserpine pharmacokinetics has been previously identified in available databases (National Center for Biotechnology Information (2025). PubChem Compound Summary for CID 5770, Reserpine. Retrieved January 13, 2025 from https://pubchem.ncbi.nlm.nih.gov/compound/Reserpine). Importantly, the drug in this study was administered intravitreally, where the ocular compartments are relatively isolated from systemic metabolism or excretion. Under these conditions, where absorption, distribution, metabolism, and excretion have minimal impact, we observed sex differences in efficacy using the same dose of drug.

Nonetheless, we agree with the reviewer and plan to pursue dose-response and other studies in future investigations.

Statistical Analysis

In my opinion, there is room for improvement. How were the animals injected? Was the contralateral eye used as control? (no information in the manuscript about it!, line 390 just mentions the volume and concentration of injections). If so, why not use parametric paired analysis? Why use a non-parametric test, as it is the Mann-Whitney U? The Mann-Whitney U test is usually employed for discontinuous count data; is that the case here?<br /> Therefore, please specify whether contralateral eyes or independent groups served as controls. If contralateral controls were used, paired parametric tests (e.g., paired t-tests) would be statistically appropriate. Alternatively, if independent cohorts were used, non-parametric Mann-Whitney U tests may suffice but require clear justification.

We apologize for the lack of clarity. In line 124, we described the injection as “bilateral intravitreal injections of 5 µL of either vehicle or 40 µM reserpine,” and in Figure 1A, we annotated the bilateral injection as DMSO for both eyes and RSP for both eyes. To address this uncertainty, we added the clarification, “with each group receiving bilateral injections of either vehicle or reserpine” (lines 404–405). Since the results are not paired and involve continuous data for which the normality assumption cannot be confidently met or verified, we used the Mann-Whitney U test for statistical analysis.

Sex-Specific Pathways

The authors do identify pathways enriched in female vs. male retinas but fail to explicitly connect these to the changes in phenotype analysed by ERG and OCT. The lack of mechanistic validation weakens the argument.

The study does not explore why female rats respond better to reserpine. Potential factors such as hormonal differences, retinal size, or differential drug uptake are not discussed.

It remains open, whether observed transcriptomic trends (e.g., proteostasis network genes) correlate with sex-specific functional outcomes.

We acknowledge that, while we identified pathways enriched in female versus male retinas, we did not explicitly connect these findings to the functional phenotypes measured by ERG and OCT. Although our transcriptomic data suggest that reserpine differentially influences pathways such as proteostasis and p53 signaling, we did not conduct mechanistic experiments to validate a causal relationship between these pathways and the observed outcomes.

In practice, designing a study to validate the mechanisms of a small molecule modulating multiple pathways presents significant challenges. If the pathways cannot be specifically modulated or if modulation could result in irreversible outcomes, the mechanistic validation becomes difficult to achieve. Drugs demonstrating mutation-agnostic efficacy are often investigated primarily through outcome measures and the analysis of affected pathways rather than through direct mechanistic validation (Leinonen, H., Zhang, J., Occelli, L. M., Seemab, U., Choi, E. H., L P Marinho, L. F., Querubin, J., Kolesnikov, A. V., Galinska, A., Kordecka, K., Hoang, T., Lewandowski, D., Lee, T. T., Einstein, E. E., Einstein, D. E., Dong, Z., Kiser, P. D., Blackshaw, S., Kefalov, V. J., Tabaka, M., … Palczewski, K. (2024). A combination treatment based on drug repurposing demonstrates mutation-agnostic efficacy in pre-clinical retinopathy models. Nature communications, 15(1), 5943. https://doi.org/10.1038/s41467-024-50033-5).

As recommended, we added potential factors that might influence the differential response to reserpine, based on other studies (lines 353–362) highlighting differences in dopamine storage capacity and estrogen independence. We also added a discussion on the possibility of sex-related differences in basal ERG response levels (lines 363–366).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The study presents compelling findings on the neuroprotective effects of reserpine in a well-established model of retinitis pigmentosa (P23H-1). The use of ERG, optomotor assays, OCT, immunohistochemistry, and transcriptomic techniques provides a good exploration of the treatment's effects, particularly highlighting the differential response in females. The study underscores the potential of drug repurposing to expedite the availability of therapeutic interventions for patients.

Thanks for your generous comments.

While the manuscript presents an important contribution, I would like to highlight a few points that need clarification or further elaboration to strengthen the work:

(1) Please include the photopic a-wave data in your analysis or provide a justification for its omission. Specifically, it would be valuable to know whether there is an improvement in this parameter under reserpine treatment.

We appreciate the reviewer’s suggestion to include photopic a-wave data in our analysis and acknowledge the importance of this parameter in evaluating cone photoreceptor function. However, we did not analyze the photopic a-wave amplitude in our study because we found the photopic a-wave has low amplitude and high variability, consistent with findings in other studies with P23H-1 rats (Orhan E, Dalkara D, Neuillé M, Lechauve C, Michiels C, et al. (2015) Genotypic and Phenotypic Characterization of P23H Line 1 Rat Model. PLOS ONE 10(5): e0127319. https://doi.org/10.1371/journal.pone.0127319) or even with wild type rats (V.L. Fonteille, J. Racine, S. Joly, A.L. Dorfman, S. Rosolen, P. Lachapelle; Do Rats Generate a Photopic a–Wave? . Invest. Ophthalmol. Vis. Sci. 2005;46(13):2246). We added the description (lines 435-437) explaining why the photopic a-wave was not analyzed. Studies with P23H-1 did not analyze the photopic a-wave, probably for similar reasons.

(2) In Figure 1, it would be helpful to include data from normal control animals to provide a benchmark for retinal degeneration in P23H-1 animals and to better contextualize the effects of reserpine treatment.

Thanks. As suggested, we have included data from normal control animals to Figure 1.

(3) The manuscript states that "Treated female retinas have significantly higher expression of the gene for P62 (SQSTM1), indicating a potential key route for reserpine's activity" (Line 331). Please explain how this difference in expression might translate into a better photoreceptor response in females compared to males.

The difference in P62 (SQSTM1) expression between treated female and male retinas could have important implications for the photoreceptor response. We have identified in our previous study that reserpine increased P62 that mediates proteome balance between ubiquitin-proteasome system (UPS) and autophagy. Together with the role of P62 in the regulation of oxidative stress, P62 might be important for photoreceptor survival and function. Higher expression of P62 in treated females could suggest more efficient cellular maintenance and a better ability to cope with stress, leading to improved photoreceptor survival and function.

(4) Numerous studies have shown that animal models of Parkinson's disease (e.g., those treated with MPTP or rotenone) or retinal tissue from Parkinson's patients exhibit dopaminergic cell death and associated vision loss. Please discuss how these findings relate to your results. Can you hypothesize how dopamine depletion by reserpine may lead to improved photoreceptor responses in your model?

We appreciate the reviewer’s insightful comments. Both MPTP and rotenone act via inhibition of complex I of the respiratory chain, causing cell death and leading to dopamine depletion. In contrast, reserpine acts by inhibiting the vesicular monoamine transporter, depleting catecholamines by preventing their storage and facilitating their metabolism by monoamine oxidase. Although reserpine and other agents can induce animal models of Parkinson's disease, reserpine differs from the others in several aspects: (i) reserpine do not induce neurodegeneration and protein aggregation; (ii) motor performance, monoamine content, and TH staining are partially restored after treatment interruption; and (iii) reserpine lacks specificity regarding dopaminergic neurotransmission (Leão, A. H., Sarmento-Silva, A. J., Santos, J. R., Ribeiro, A. M., & Silva, R. H. (2015). Molecular, Neurochemical, and Behavioral Hallmarks of Reserpine as a Model for Parkinson's Disease: New Perspectives to a Long-Standing Model. Brain pathology (Zurich, Switzerland), 25(4), 377–390. https://doi.org/10.1111/bpa.12253). We have discussed the various effects of catecholamine depletion on retinal diseases (lines 331–337). Both dopamine receptor antagonists and agonists, as well as catecholamine depletion, can exert protective effects on the retina. The reduction in scotopic b-wave amplitude observed at P54, followed by a lack of further progression in degeneration, may support the hypothesis that reduced neuronal activity due to catecholamine depletion could have mitigated damage to retinal neurons.

(5) For readers who may not be familiar with the P23H-1 mutation, it would be beneficial to include a brief description of the timeline and progression of retinal degeneration in this model.

As the progression varies among studies, we have provided our description on observations from the same facility where the animals were housed. The timeline and progression of retinal degeneration are briefly described in the results section (lines 112–115) and Supplementary Figure 1.

(6) Do you have any data on the effects of reserpine treatment in older animals? If available, this could provide additional insight into the potential applicability of reserpine in later stages of disease progression.

Unfortunately, we do not have data from older animals. As described in the results section (lines 116–124), we set the timepoint for interventions before functional impairment peaked, aiming to harness the remaining potential for rescue and promote functional improvement. Our approach focused on developing a gene-agnostic therapy that can delay disease progression and be delivered at an earlier stage than AAV-based therapies, using FDA-approved drugs.

(7) Molecular Basis of Sex Differences: The molecular mechanisms underlying the differential responses in males and females should be elaborated upon. If possible, include a discussion or hypothesis that addresses these sex-specific differences at the molecular level.

We thank the reviewer for highlighting the importance of addressing the molecular basis of sex-specific differences. In our study, we observed distinct transcriptomic responses to reserpine between male and female rats, particularly in molecular pathways related to proteostasis and p53 signaling. While the sex-specific differences in these molecular pathways remain to be fully evaluated, we have added a discussion on sex differences in reserpine responses, incorporating findings from other studies (lines 353–366).

Reviewer #2 (Recommendations for the authors):

(1) There is no mention in the manuscript about the fact that the transgene rats have several copies of rhodopsin and how this can affect these sex differences. Would it be the same in the P23H KO mouse? Or in other models with a single copy of the mutation?

We have described in the Materials and Methods section how they were bred, but we did not specifically mention the allele status in the manuscript. Hemizygous P23H-1 rats used in this study carry a single P23H transgene allele with a transgene copy number of 9, in addition to the normal two wild-type opsin alleles. We added this description to clear the uncertainty (lines 384-387.

(2) This sentence: in abstract lines 26 to 29: "Recently, we identified reserpine as a lead molecule for maintaining rod survival in mouse and human retinal organoids as well as in the rd16 mouse, which phenocopy Leber congenital amaurosis caused by mutations in the cilia-centrosomal gene CEP290 (Chen et al. eLife 2023;12:e83205. DOI: https://doi.org/10.7554/eLife.83205)", to my vew, does not belong to the abstract, maybe in the introduction as stage of art.

Thank you for asking. According to the guidelines for the research advance articles (that follow previously published studies), a reference to the original eLife article should be included in the abstract. As specified in the guidelines, we have updated the citation format to (author, year) for referencing eLife articles (line 29).

(3) Lines 167-170: "Histologic evaluation of the retinas also demonstrated more prominent ONL thinning in the dorsal retina and increased ONL thickness in the dorsal retina measured at 1,000, 1,250, and 1,500 µm distant from the optic nerve head in reserpine-treated group compared with control group (Figure 3C)". I do not understand this sentence. Is it a more prominent thinning or an increased thickness?

We apologize for the confusion caused by this sentence. The histological evaluation showed that ONL thinning was more pronounced in the dorsal retina of control group, which was consistent with OCT findings in Figure 3A. Reserpine treatment increased the ONL thickness in the dorsal retina at specific distances from the optic nerve head (1,000, 1,250, and 1,500 µm). We have revised the sentence for clarity (lines 165-168).

(4) Lines 182-185 and Figure 4B: FL is not the best approach to quantify rhodopsin levels. Since the DAPI staining is overexposed, it is hard to evaluate the staining of RHO in the ONL. From the visible staining in the OS, it is only possible to affirm that the OS are longer in RSP-treated retinas... more is not to be affirmed based on these figures. I suggest using WB.

We acknowledge the reviewer’s concern regarding the use of fluorescence imaging to quantify rhodopsin levels. While our current data highlight structural preservation, such as the length of the outer segments, we agree that drawing conclusions about rhodopsin levels from fluorescence staining is limited. As we do not have samples for WB and fluorescence imaging cannot quantify rhodopsin, we have revised the description (lines 180-184).

(5) Lines 188-190 and Figure 4C: The images in 4C showed an extreme divergence between treated and untreated retina concerning the amount of stained cones, which is not observed at the quantification at 1000µm statistic. Are the images not representative?

We agree with the reviewer that the images in Figure 4C may not adequately represent the quantified data. To address this, we have changed the figure to reflect the quantification results accurately.

(6) Figures 6C-6D and 6G. Why do the authors not use any statistical analysis? Or are the differences not statistically significant? Why do authors use only WT and DMSO controls? What about untreated P23H controls (no DMSO)?

Thanks for checking, and we apologize for the oversight. We have updated figures 5, 6 and S5 to include adjusted p-value in relevant plots. In addition, details of significance threshold are available in supplementary tables. Regarding controls, untreated P23H retinas (without DMSO) were not included in the current analysis, as our experience shows that DMSO injection itself does not cause functional or structural changes. The key data demonstrating the effect of reserpine involve a comparison between the group treated with reserpine and the control group treated with DMSO, as the only difference between these groups is the involvement of the drug.

(7) Validation of findings by testing key genes (e.g., p62/SQSTM1, Nrf2) using qPCR or immunohistochemistry will strengthen the findings.

We appreciate the reviewer’s suggestion to validate key findings using qPCR or immunohistochemistry, as such experiments are crucial for further strengthening our conclusions. While this was not feasible in the current study due to various constraints, we fully recognize their importance and plan to incorporate these in our follow-up studies.

Author response:

The following is the authors’ response to the previous reviews

Response to Public Reviews:

We would like to thank the reviewers and editors once more for their time and effort in reviewing our manuscript. Below we discuss specifically our response to the recommendations of Reviewer 2, which were the only substantial changes we made to the manuscript.

Reviewer 2 recommendation:

"My only remaining suggestion is that the authors acknowledge and cite the work of other groups which have similarly found different subsets of LADs based on various molecular/epigenetic features:

(1) doi.org/10.1101/2024.12.20.629719

(2) PMID: 25995381

(3) PMID: 36691074

(4) PMID: 23124521 (fLADs versus cLADs, as described by the authors themselves) The exact subtypes of LADs might be different based on the features examined, but others have found/implicated the existence of different types of LADs. Hence, the pwv-LAD should be contextualized within these findings (which they do relative to v-fiLADs)."

We thank the reviewer for this suggestion and for these references. We think that the best place to go into depth about how our work relates to these references would be in an appropriate review article.

However, we did read these references carefully and responded, as described below, by adding additional clarifying text in the manuscript as well as mention of articles specifically relevant to our description of our results.

(1) Reviewer 2 wrote specifically, "Hence, the pwv-LAD should be contextualized within these findings (which they do relative to v-fiLADs)"

We are not sure exactly what Reviewer 2 means here. In this manuscript we defined p-w-v iLADs, not LADs. So, it would be inappropriate to compare a subset of iLAD regions with different types of LADs.

If this was the meaning of Reviewer 2, then other readers might have similar confusion. Therefore, we added the following clarifying text in red:

"Several previous studies have used varying approaches to subdivide LADs further into distinct subsets of LADs with different biochemical and/or functional properties (Martin et al., 2024; Meuleman et al., 2013; Shah et al., 2023; Zheng et al., 2015). However, in this Section we focused instead on asking whether regions specifically within iLADs might show differential localization relative to the lamina and/or nucleoli and, if so, whether these regions would show different levels of gene expression. More specifically, analogously to how gene expression hot-zones appeared as local maxima in speckle TSA-seq with early DNA replication timing, we asked whether iLAD regions that appeared as local maxima in lamina proximity mapping signals would correspond to iLAD regions with locally reduced gene expression levels and later DNA replication timing relative to their flanking iLAD sequences. Our rationale was that these iLAD regions might represent chromatin domains that together with their flanking iLAD regions would typically localize well within the nuclear interior but in a fraction of the cell population would loop back and attach at the nuclear periphery."

(2) We also added the following text near the end of the section about p-w-v iLADs to place them in the context of one class of "LADs" identified by ChIP-seq rather than DamID. We use quotation marks since the approach used produced a segmentation that included a nearly 50/50 mix of iLAD and LAD regions, as identified by DamID, for this class of domains.

"We note that in a previous study a three-state Hidden Markov Model (HMM) segmented lamin B ChIP-seq data into two chromatin domain states with extensive overlap with LADs defined by lamina DamID (Shah et al., 2023). Whereas the late replicating, low gene density/expression "T1 LAD" state showed very high overlap (98%) with LADs defined by DamID, the intermediate replicating, intermediate gene expression "T2 LAD" state showed only 47% overlap with LADs defined by DamID. This was partly a result of the HMM segmentation algorithm but also due to substantial differences between the lamina ChIPseq versus DamID signals for reasons that remain unclear. The subset of p-w-v iLADs included in T2 comprise only a small percentage of the total T2 LAD coverage, which includes both other iLAD and LAD regions. Thus, the p-w-v iLADs we identified here represent a novel and distinct class of iLAD chromatin domains, not previously described."

(3) Alternatively, what Reviewer 2 might be suggesting implicitly is that we should start with the regions identified as p-w-v iLADs in one cell type and then identify all of those p-w-v iLADs which instead exist as LADs in a second cell type. Once we have identified their LAD equivalents in a second cell type we could then ask whether they possess special characteristics such that they correspond to a specific type of LAD subset. Finally, we could then ask how that specific type of LAD subset compared to the different subtypes of LADs identified by other groups and, in particular, the references Reviewer 2 provided.

We agree that would be an interesting future direction, but we consider that as outside the scope of this current manuscript. We note that we did no such analysis of the characteristics of LADs which existed as p-w-v iLADs in a different cell line. We save that for a possible future analysis, ideally in the same cell types as used in the cited references to allow a more direct comparison.

(4) Finally, we added text in the Discussion that relates our analysis of the differential SON and LMNB1 TSA-seq signals for different LAD regions, and how these correlate with different histone modifications, with results from the recent preprint cited by Reviewer 2. Note that we could not directly correlate our results from human cells with the three classes of LADs described in MEFs by this preprint.

"Fourth, we show how LAD regions showing different histone marks- either enriched in H3K9me3, H3K9me2 plus H2A.Z, H3K27me3, or none of these marks- can differentially segregate within nuclei. These results support the previous suggestion of different "flavors" of LAD regions, based on the sensitivity of the autonomous targeting of BAC transgenes to the lamina to different histone methyltransferases (Bian et al., 2013). Differential nuclear localization also was recently inferred by the appearance of different Hi-C Bsubcompartments, which similarly were differentially enriched in either H3K9m3, H3K27me3, or the combination of H3K9me2 and H2A.Z (Spracklin et al., 2023). More recently, and while this paper was in revision, a new study described segmenting mouse embryonic fibroblast LADs into three clusters using histone modification profiling (Martin et al., 2024). Interestingly, these three LAD clusters also most notably differed by their dominant enrichment of either H3K9me3, H3K9me2, or H3K27me3. Thus, three orthogonal approaches have converged on identifying different LAD regions showing differential enrichment either of H3K9me3, H3K9me2, or H3K27me3. Here, our use of TSA-seq directly measures and assigns the intranuclear localization of these different LAD regions to different nuclear locales."

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Gray and colleagues describe the identification of Integrator complex subunit 12 (INTS12) as a contributor to HIV latency in two different cell lines and in cells isolated from the blood of people living with HIV. The authors employed a high-throughput CRISPR screening strategy to knock down genes and assess their relevance in maintaining HIV latency. They had used a similar approach in two previous studies, finding genes required for latency reactivation or genes preventing it and whose knockdown could enhance the latency-reactivating effect of the NFκB activator AZD5582. This work builds on the latter approach by testing the ability of gene knockdowns to complement the latency-reactivating effects of AZD5582 in combination with the BET inhibitor I-BET151. This drug combination was selected because it has been previously shown to display synergistic effects on latency reactivation.

The finding that INTS12 may play a role in HIV latency is novel, and the effect of its knockdown in inducing HIV transcription in primary cells, albeit in only a subset of donors, is intriguing. However, there are some data and clarifications that would be important to include to complement the information provided in the current version of the manuscript.

We have now added the requested data and clarifications. In particular, we show that knockout of INTS12 has no effect on cell proliferation (new data added in Figure 2—figure supplement 3)), we clarify how the degree of knockout and the complementation were accomplished, we clarify the differences between the RNA-seq and the activation scores, and we have bolstered the claim that INTS12 affected transcription elongation by performing CUT&Tag on Ser2 phosphorylation of the C-terminal tail of RNAPII along the length of the provirus (new data added in Figure 5C) Please see detailed responses below.

Reviewer #2 (Public review):

Summary:

Identifying an important role for the Integrator complex in repressing HIV transcription and suggesting that by targeting subunits of this complex specifically, INTS12, reversal of latency with and without latency reversal agents can be enhanced.

Strengths:

The strengths of the paper include the general strategy for screening targets that may activate HIV latency and the rigor of exploring the mechanism of INTS12 repression of HIV transcriptional elongation. I found the mechanism of INTS12 interesting and maybe even the most impactful part of the findings.

Weaknesses:

I have two minor comments:

There was an opportunity to examine a larger panel of latency reversal agents that reactivate by different mechanisms to determine whether INTS12 and transcriptional elongation are limiting for a broad spectrum of latency reversal agents.

I felt the authors could have extended their discussion of how exquisitely sensitive HIV transcription is to pausing and transcriptional elongation and the insights this provides about general HIV transcriptional regulation.

We have now added data on latency reversal agents of different mechanisms of action. We show that INTS12 affects HIV latency reversal from agents that affect the non-canonical NF-kB pathway (AZD5582), the canonical NF-kB pathway (TNF-alpha), activation via the T-cell receptor (CD3/CD28 antibodies), through bromodomain inhibition (I-BET151), and through a histone deacetylase inhibitor (SAHA). This additional data has been added to the manuscript in Figure 7, panels B and C as well as adding text to the discussion.

We appreciate the suggestion to extend the discussion to emphasize how important pausing and elongation are to HIV transcription. Additionally, to further support our claim that INTS12KO with AZD5582 & I-BET151 leads to an increase in elongation, that we previously showed with CUT&Tag data showing an increase in total RNAPII seen in within HIV (Figure 5B), we measured RNAPII Ser2 phosphorylation (Figure 5C) and RNAPII Ser5 phosphorylation (Figure 5—figure supplement 2) and added these findings to the manuscript. Upon measuring Ser2 phosphorylation, a marker associated with elongation, we observed evidence of elongation-competent RNAPII in our AZD5582 & I-BET151 condition as well as our INTS12 KO with AZD5582 & I-BET151 condition, as we saw an increase of Ser2 phosphorylation within HIV. Despite seeing elongation-competent RNAPII in both conditions, we only saw a dramatic increase in total RNAPII for our INTS12 KO and AZD5582 & I-BET151 condition (Figure 5B), which supports that there are more elongation events and that an elongation block is overcome specifically with INTS12 KO paired with AZD5582 & I-BET151. This claim is further supported by our data showing an increase in virus in the supernatant only with the INTS12 KO with AZD5582 & I-BET151 condition in cells from PLWH (Figure 6C). We did not observe any statistically significant differences between RNAPII Ser5 phosphorylation, which might be expected as this mark is not associated with elongation (Figure 5—figure supplement 2).

Reviewer #3 (Public review):

Summary:

Transcriptionally silent HIV-1 genomes integrated into the host`s genome represent the main obstacle to an HIV-1 cure. Therefore, agents aimed at promoting HIV transcription, the so-called latency reactivating agents (LRAs) might represent useful tools to render these hidden proviruses visible to the immune system. The authors successfully identified, through multiple techniques, INTS12, a component of the Integrator complex involved in 3' processing of small nuclear RNAs U1 and U2, as a factor promoting HIV-1 latency and hindering elongation of the HIV RNA transcripts. This factor synergizes with a previously identified combination of LRAs, one of which, AZD5582, has been validated in the macaque model for HIV persistence during therapy (https://pubmed.ncbi.nlm.nih.gov/37783968/). The other compound, I-BET151, is known to synergize with AZD5582, and is a inhibitor of BET, factors counteracting the elongation of RNA transcripts.

Strengths:

The findings were confirmed through multiple screens and multiple techniques. The authors successfully mapped the identified HIV silencing factor at the HIV promoter.

Weaknesses:

(1) Initial bias:

In the choice of the genes comprised in the library, the authors readdress their previous paper (Hsieh et al.) where it is stated: "To specifically investigate host epigenetic regulators involved in the maintenance of HIV-1 latency, we generated a custom human epigenome specific sgRNA CRISPR library (HuEpi). This library contains sgRNAs targeting epigenome factors such as histones, histone binders (e.g., histone readers and chaperones), histone modifiers (e.g., histone writers and erasers), and general chromatin associated factors (e.g., RNA and DNA modifiers) (Fig 1B and 1C)".

From these figure panels, it clearly appears that the genes chosen are all belonging to the indicated pathways. While I have nothing to object to on the pertinence to HIV latency of the pathways selected, the authors should spend some words on the criteria followed to select these pathways. Other pathways involving epigenetic modifications and containing genes not represented in the indicated pathways may have been left apart.

(2) Dereplication:

From Figure 1 it appears that INTS12 alone reactivates HIV -1 from latency alone without any drug intervention as shown by the MACGeCk score of DMSO-alone controls. If INTS12 knockdown alone shows antilatency effects, why, then were they unable to identify it in their previous article (Hsieh et al., 2023)? The authors should include some words on the comparison of the results using DMSO alone with those of the previous screen that they conducted.

(3) Translational potential:

In order to propose a protein as a drug target, it is necessary to adhere to the "primum non nocere" principle in medicine. It is therefore fundamental to show the effects of INTS12 knockdown on cell viability/proliferation (and, advisably, T-cell activation). These data are not reported in the manuscript in its current form, and the authors are strongly encouraged to provide them.

Finally, as many readers may not be very familiar with the general principles behind CRISPR Cas9 screening techniques, I suggest addressing them in this excellent review: https://pmc.ncbi.nlm.nih.gov/articles/PMC7479249/.

(1) The CRISPR library used was more completely described in a previous publication (Hsieh et al, PLOS Pathogens, 2023). However, we now more explicitly refer the reader to information about the pathways targeted in the library. We also point out how initial hits in the library lead to finding genes outside of the starting library as in the follow-up screen in Figure 7 where each of the members of the INT complex are interrogated even though only INTS12 was the only member in the initial library.

(2) We understand the confusion between the hits in this paper and a previous publication. Indeed, INTS12 was observed in Hsieh et al., PLOS Pathogens, 2023 as a hit in the Venn diagram of Figure 3B of that paper, and in Figure 5A, right panel of that paper. However, it was not followed up on in the previous paper since that paper focused on a hit that was unique to increasing the potency of one particular LRA. We added text to the present manuscript to make it clear that the screens identified many of the same hits. We have also added additional data here on hit validation to underscore the reliability of the CRISPR screen. In one of the cell lines (5A8), EZH2 was a strong hit (Figure 1B). We have now added data that shows that an inhibitor to EZH2 augments the latency reversal of AZD5582/I-BET151 as predicted from the screen. This data has been added to Figure 1, figure supplement 1.

(3) We appreciate the concern that for INTS12 to be a drug target, it should not be essential to cell viability. We now show that knockout of INTS12 has no effect on cell proliferation (new data added in Figure 2—figure supplement 3). In addition, the discussion now adds additional literature references that describe how knockout of INTS12 has relatively minor effects on cell functions in comparison to knockout of other INT members which supports that the proposal that modulation of INTS12 may be more specific than targeting the catalytic modules of Integrator. Nonetheless, we completely agree with the reviewer that many other aspects of how INTS12 affects T cell functions have not been addressed as well as other potential detrimental effect of INTS12 as a drug target in vivo. We now more explicitly describe these caveats in the discussion but feel that the present manuscript is a first step with a long path ahead before the translational potential might be realized.

(4) We now cite the review of CRISPR screens suggested by the reviewer.

Responses to recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The authors report in the legend of Figure 2 (and similarly in other figures) that there was "a calculated INTS12 knockout score of 76% (for the one guide used) and 69% (for one of three guides used), respectively." However, it would be helpful to show representative data on the efficiency of INTS12 knockdown in cell lines and primary cells, as well as data on the efficiency of the complementation (Figure 2C).

The knockout scores cited are the genetic assays for the efficiency based on sequence files. As the knockouts are done with multiple guides the knockout for each guide is an underestimate of the total knockout. The complementation, however, was done by adding back INTS12 in a lentiviral vector that also contains a drug resistance marker (puromycin). Cells were then selected for puromycin resistance, and therefore, all of them contain the complemented gene. What one would ideally like is a Western blot to quantify the amount of INTS12 remaining in the knockout pools. Unfortunately, despite obtaining multiple different commercial sources of INTS12 antibodies, we were unable to identify one that was suitable for Western blotting (as opposed to two that did work for CUT&Tag). Nonetheless, the functional data in primary T cells from PLWH and in J-Lat cells lines does show the even if the knockout is suboptimal, we find activation after INTS12 knockout (e.g., Figure 6).

(2) Flow cytometry methods are not reported, but was a viability dye included when testing GFP reactivation (Figure S2)? More broadly, showing data on the viability of cells post-knockdown and drug treatments would help, as cell mortality is inherently associated with latency reactivation in J-Lat cells. For the same reason, reporting viability data would be important for primary cells, as the electroporation procedure can lead to significant mortality.

We did not include viability dyes in the data for GFP activation. However, as described in the public response, we have done growth curves in J-Lat 10.6 cells with and without INTS12 knockout and find no effects on cell proliferation (Figure 2—figure supplement 3). As the reviewer points out, it is not possible to do these experiments in primary cells since the electroporation itself causes a degree of cell death. Nonetheless, we do see effects on HIV activation in these primary cells (Figure 6).

(3) Figure S2 shows a relatively high baseline expression (approximately 15%) of HIV-GFP, which is not unusual for the J-Lat 10.6 clone. However, Figure 3 appears to show no HIV RNA reads in the control condition of this same cell clone. How do the authors reconcile this discrepancy?

We believe that the discrepancies in the flow cytometry versus RNA-seq assays are due to differences in the sensitivity of the assays, the linear range of the assays especially at the lower end, and the different half-lives of RNA versus protein. We now clarify that Figure 3 does not show “no” HIV RNA at baseline, but rather values of ~30 copies per million read counts. This increases to ~800 copies per million read counts when INTS12 knockout cells are treated with AZD5582/I-BET151. These values have the same fold change predicted in Figure 4, and more closely resemble the trend in Figure 2—figure supplement 1.

(4) The combination of AZD5582 and I-BET151 consistently reactivates HIV latency (including GFP protein expression), as previously reported and as shown here by the authors. However, in Figure 5B, RPB3/RNAPII occupancy in the DMSO control appears higher than in the AAVS1KO + AZD5582 and I-BET151 samples. This should be discussed, as it could raise concerns about the robustness of RPB3/RNAPII occupancy results as a proxy for provirus elongation.

As addressed in the public comments, in order to strengthen our claims about transcriptional elongation control, we measured RNAPII Ser2 and Ser5 phosphorylation levels. We see evidence of elongation with Ser2 in the condition of concern (AAVS1 KO + AZD5582 & I-BET151) as well as our main condition of interest (INTS12 KO + AZD5582 & I-BET151) and no change in Ser5 for any condition. With both the Ser2 phosphorylation and total RNAPII as well as our virus release and transcription data we believe that we are seeing evidence of increased elongation with INTS12 KO with AZD5582 & I-BET151. One potential nuance that may not be gathered from the CUT&Tag data is the turnover rate of the polymerase. Despite the levels of RNAPII appearing lower in the condition of concern (AAVS1 KO + AZD5582 & I-BET151) compared to DMSO it is possible that low levels of elongation are occurring but that in our INTS12 KO + AZD5582 & I-BET151 condition there is more rapid elongation and this is why we can observe more RNAPII within HIV. This new data is added in Figure 5C and Figure 5—supplement 2 and its implications are now described in more detail in the discussion.

(5) The authors write that "Degree of reactivation was correlated with reservoir size as donors PH504 (star symbol) and PH543 (upside down triangle) have the largest HIV reservoirs (supplemental Figure S2)." I could not find mention of the reservoir size of these donors in the figure provided.

This confusion was caused by mislabeling of the supplement number, which we fixed, and we added additional labeling to make finding the reservoir size even more clear as this is an important part of the manuscript. This is now found in Supplemental file S4.

Reviewer #3 (Recommendations for the authors):

(1) The MAGeCK gene score is a feature that is essential for the interpretation of the results in Figure 1. The authors do quote the Li et al. paper where this score was described for the first time (https://genomebiology.biomedcentral.com/articles/10.1186/s13059-014-0554-4), however, they may understand that not all readers may be familiar with this score. Therefore a didactic short description of this score should be done when introducing the results in Figure 1.

We have added a short description to the paper to address this.

(2) Figure 4. The authors write: "Among the host genes most prominently affected by INTS12 knockout with AZD5582 & I-BET151 are MAFA, MAFB, and ID2 (full list of genes in supplemental file S3)." I am a bit confused. In the linked Excel file there is only a list of a few genes. The differentially expressed genes appear to be many more from Figure 4. The full list should be uploaded.

We believe there was a mistake in our original uploading and naming of the supplements. We have now double-checked numbering on the supplements and added in text clarification of which excel tabs hold the desired information.

(3) Figure 6: The authors are right in highlighting that there is a high level of variability in viral RNA in supernatants in the early stages of viral reactivation. It is therefore advisable to repeat measurements at Day 7, at which variability decreases and data are more reliable (please, see: https://www.thelancet.com/journals/ebiom/article/PIIS2352-3964(23)00443-7/fulltext).

While it would have been nice to prolong these measurements, our current assay conditions are not optimal for longer term growth of the cells. We note that the measurements were all done in biological triplicates (independent knockouts) and in different individuals. Because the number of activatable latent proviruses is variable and the number of cells tested is limiting, the variability in the assays is expected.

(4) Figure 7: The main genes outside the INTS family should be identified, also.

We include the full list in supplemental file S5 and sort by most enriched.

(5) Methods: A statistical paragraph should be added in the Methods section, detailing the data analysis procedures and the key parameters utilized (for example, which is the MAGeCK gene score threshold that they used to consider knockdown efficacy on HIV latency?).

There is no MAGeCK score threshold that we use to determine efficacy on HIV latency. In a previous publication using CRISPR screens for HIV Dependency Factors (Montoya et al, mBio 2023), we showed that there is a relationship between the MAGeCK and the effect of that gene knockout on HIV replication (Figure 5 that paper). However, it is a continuum rather than a strict threshold and we believe that the effects on HIV latency would respond similarly. In the current paper, we have focused on the top hits rather than a comprehensive analysis of all the entire list. In case the reviewer is referring to the average and standard deviation of the non-targeting controls, we have added this to the figure legend and methods.

Author response:

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

Public Reviews: 

Reviewer #1 (Public review): 

Summary:  

The study identifies two types of activation: one that is cue-triggered and nonspecific to motion directions, and another that is specific to the exposed motion directions but occurs in a reversed manner. The finding that activity in the medial temporal lobe (MTL) preceded that in the visual cortex suggests that the visual cortex may serve as a platform for the manifestation of replay events, which potentially enhance visual sequence learning.  

Strengths: 

Identifying the two types of activation after exposure to a sequence of motion directions is very interesting. The experimental design, procedures, and analyses are solid. The findings are interesting and novel. 

Weaknesses: 

It was not immediately clear to me why the second type of activation was suggested to occur spontaneously. The procedural differences in the analyses that distinguished between the two types of activation need to be a little better clarified.  

We thank the reviewer for his/her summary and constructive feedback on our study. We appreciate the recognition of the strengths of our study.

The second type of activation, namely the replay of feature-specific reactivations, is considered spontaneous because it reflects internally driven neural processes rather than responses directly triggered by external stimuli. Unlike responses evoked by stimuli, spontaneous replay is not time-locked to stimulus onset. Instead, it arises from the brain's intrinsic activity, typically observed during offline periods (e.g., rest or blank period) when external stimuli are absent. This allows the neural system to reactivate and consolidate prior experiences without interference from ongoing external stimuli.

Replay is believed to be a key mechanism underlying various cognitive functions, such as memory consolidation (Gillespie et al., 2021; Gridchyn et al., 2020), learning (Igata et al., 2021), prediction and planning (Ólafsdóttir et al., 2018). Furthermore, the hippocampus and related cortical areas engage in replay to extract abstract relationships from sequential experiences, forming a "template" that can generalize across contexts (Liu et al., 2019). In our study, the feature-specific replay observed during blank periods likely reflects this process, supporting the integration of exposed motion direction sequences into cohesive memory representations and facilitating visual sequence learning.

We have extended the Discussion section to incorporate this explanation (Lines 440 - 447).

Regarding the second question, the procedural differences between the two types of activations lie in the classifiers used for the two analyses: a multiclass classifier for non-specific elevated responses and binary classifiers for feature-specific replay. 

For the non-feature-specific elevated responses, we trained a five-class (with the labels of the four RDKs and the ITI (inter-stimulus interval)) classifier on the localizer data and tested on the blank period in the main phase. We attempted to decode motion direction information at each time point at the group level. However, the results revealed no feature-specific information at the group level during the blank period.

For the feature-specific replay, we employed the temporal delayed linear modeling (TDLM) to examine whether individual motion direction information was encoded in a sequential and spontaneous manner. Here, we first needed to train four binary classifiers, each was sensitive to only one motion direction (i.e., 0°, 90°, 180°, or 270°), as our aim was to quantify the evidence of feature-specific sequence in the subsequent analyses. For each classifier, positive instances were trials where the corresponding feature (e.g., 0°) was presented, while negative instances included trials with other features (e.g., 90°, 180°, and 270°) and an equivalent amount of null data from the ITI period (1–1.5 s).

We have clarified these methodological details in the Methods section (Pages 34 – 41).

Reviewer #2 (Public review): 

This paper shows and analyzes an interesting phenomenon. It shows that when people are exposed to sequences of moving dots (that is moving dots in one direction, followed by another direction, etc.), showing either the starting movement direction or ending movement direction causes a coarse-grained brain response that is similar to that elicited by the complete sequence of 4 directions. However, they show by decoding the sensor responses that this brain activity actually does not carry information about the actual sequence and the motion directions, at least not on the time scale of the initial sequence. They also show a reverse reply on a highly compressed time scale, which is elicited during the period of elevated activity, and activated by the first and last elements of the sequence, but not others. Additionally, these replays seem to occur during periods of cortical ripples, similar to what is found in animal studies. 

These results are intriguing. They are based on MEG recordings in humans, and finding such replays in humans is novel. Also, this is based on what seems to be sophisticated statistical analysis. However, this is the main problem with this paper. The statistical analysis is not explained well at all, and therefore its validity is hard to evaluate. I am not at all saying it is incorrect; what I am saying is that given how it is explained, it cannot be evaluated. 

We thank the reviewer’s detailed evaluation as well as the acknowledgment of the novelty of our study.

To address the concern about the statistical analysis, in the revised manuscript, we have modified the Methods section to provide a more detailed explanation of the analytical pipeline, particularly for several important aspects such as decoding probability and TDLM. (Lines 646 – 657, Lines 682 – 734). 

Below, we provide point-by-point responses to further elaborate on these revisions and address the reviewer’s comments.

Recommendations for the authors: 

Reviewer #1 (Recommendations for the authors): 

I have questions.  

(1) Participants were exposed to a predefined sequence of motion directions either clockwise or counterclockwise. Is it possible that the observed replay is related to the activation of MST neurons? If a predetermined sequence is not in either clockwise or counterclockwise but is randomly determined like 0{degree sign}->180{degree sign}->270{degree sign}->90{degree sign}, would the same result be obtained?  

We thank the reviewer for these thoughtful questions.

First, regarding the potential involvement of MST neurons, it is plausible that the observed replay might involve activity in motion-sensitive brain regions, including the medial superior temporal (MST) and even middle temporal (MT) areas. MST neurons, located in the extrastriate visual cortex, are highly direction-selective and are known for their sensitivity to complex motion patterns, such as rotations and expansions (Duffy & Wurtz, 1991; Saito et al., 1986). In our experiment, the use of RDKs with four distinct motion directions might elicit responses in MST neurons. However, due to the limited spatial resolution of MEG, we cannot provide direct evidence for this claim. 

Second, regarding the impact of randomly ordered sequences, we believe that the replay patterns would still occur even if the sequences were randomly ordered (e.g., 0° → 180° → 270° → 90°). After a sequence is repeatedly exposed, the hippocampus has the capacity to encode abstract relationships in the sequence. Evidence supporting this view comes from previous studies. For example, Liu et al., (2019) showed that replay does not merely recapitulate visual experience but can also follow a sequence implied by learned abstract knowledge. In their study, participants were instructed that viewing pictures C→D, B→C, and A→B implies a true sequence of A→B→C→D. During subsequent testing, they observed replay events following this learned true sequence, even with novel visual stimuli, indicating that the brain maintains sequence knowledge independent of specific stimuli. Similarly, Ekman et al., (2023) showed that prediction-based neural responses could be observed when moving dots were presented in a random order rather than in a clockwise or counterclockwise order, which correspond to the four motion directions in our study. 

Together, these studies suggest that replay mechanisms in the brain are flexible and can encode and reproduce abstract relationships between sequential stimuli, regardless of their specific spatial contents. Therefore, we believe that even if the sequence were randomly ordered, the same backward replay pattern would still be observed.

(2) Is it possible that the motion direction non-specific responses actually reflect the replay of another feature of the exposed sequence, namely, the temporally rhythmic presentations of the sequence, rather than suggested in the discussion?  

We thank the reviewer for raising this insightful possibility.

There is substantial evidence that rhythmic stimulation can entrain neural oscillations, which in turn facilitates predictions about future inputs and enhances the brain's readiness for incoming stimuli (Barne et al., 2022; Herrmann et al., 2016; Lakatos et al., 2008, 2013). In our study, the temporally rhythmic presentation of the motion sequence may have entrained oscillatory activity in the brain, leading to periodic activation of sensory cortices. This rhythmic entrainment could account for the observed nonspecific responses by reflecting the brain's temporal predictions rather than specific feature replay. 

It is important to note that, however, this interpretation is in line with our initial explanation that the non-feature-specific elevated responses likely reflect a general facilitation of neural processes for any upcoming stimuli, rather than being tied to specific stimuli. The rhythmic entrainment mechanism provides another way to understand how the temporal structure in the sequences might contribute to the non-feature-specific elevated responses.

We have revised the Discussion section to incorporate this interpretation, providing a more comprehensive account for the non-feature-specific elevated responses (Lines 428 – 439).

Reviewer #2 (Recommendations for the authors): 

The main problem with the paper is that the sophisticated statistical methodology is not explained well and therefore its validity is hard to evaluate. I am not at all saying it is incorrect, what I am saying is that given how it is explained, it cannot be evaluated.  

See below for detailed point-by-point responses.  

The first part is clear. There are 4 directions of motion, and there can also be a blank screen. The random decoding accuracy would be 20%. The decoding methods from the sensors yielded a little above 50% accuracy. This is clearly about chance, but much less than one would get from electrode recording of motion-selective cells in the cortex. However, the concept and methods used here seem clear, in contrast to what comes next.  

Indeed, in the first step, we aimed to validate the reliability of our decoding model by applying a leave-one-out cross validation scheme to the localizer data. Our results showed that the decoding accuracy exceeded 50%, demonstrating robust decoding performance. However, due to the noninvasive nature of MEG and its low spatial resolution, the recorded signals represent population-level activity that inherently includes more noise compared to electrode recordings of motion-selective neurons. Therefore, the decoding accuracy in our study is understandably lower than that obtained with electrode recordings.

Next, and most of the paper relies on this concept, they use the term decoding probability (Figure 2). What is the decoding probability measure (Turner 2023)? This is not explained in the methods section. I scanned the Turner et al 2023 paper referenced and could not find the term decoding probability there. In short, I have no idea what this means. What are these numbers between 0-0.3? How does this relate to accuracies above 50% reported? This is an important concept here, and it is used throughout the paper, so it makes it hard to evaluate the paper.  

We apologize for the lack of clarity in our explanation of the term "decoding probability." Specifically, we used a one-versus-rest Lasso logistic regression model trained on the localizer data to decode the MEG signal patterns elicited by each motion direction during the main phase. The trained model could be used to predict a single label at each time point for each trial (e.g., labels 1 – 4 correspond to the four motion directions and label 5 corresponds to the ITI period). By comparing the predicted label with the true label across test trials, we could compute the time-resolved decoding accuracy as final reports.

Alternatively, rather than predicting a single label for each time point and each trial, the model can also output the probabilities associated with each label/class (e.g., we used the predict_proba function in scikit-learn). This results in a 5-column output, where each column represents the probability of the corresponding class, and the sum of the probabilities across the five columns equals 1. Finally, at each time point, averaging these probabilities across trials yields five values that indicate the likelihood of the predicted stimulus belonging to each class.

For example, Figure 2 in the manuscript depicts the decoding probabilities for the four RDKs (the probabilities for the ITI class are not shown in the figure). The number in a cell (between 0 and 0.3) indicates the probability of each class at a given time point (Figure 2A). The decoding probability does not have a direct relationship with the decoding accuracy. However, since there are five classes, the chance level of the decoding probability is 0.2. The highest probability among the five classes at a given time point determines the decoded label when computing the decoding accuracy.

For illustration, in the left panel of Figure 2B, at the onset of the first RDK (0 s), the mean decoding probabilities for the classes 0°, 90°, 180°, 270°, and the blank ITI are 5%, 4.1%, 4.0%, 4.5%, and 82.4%, respectively. Thus, the decoded label should be the blank ITI. In contrast, 0.4 s after the onset of the first RDK, the mean decoding probabilities for the five classes are 28.0%, 19.0%, 22.8%, 21.2%, and 9.0%, respectively. Therefore, the decoded label should be 0°.

We have revised the Methods section to explain this issue (Lines 646 – 657).

They did find compressed reversed reply events (Figures 3-4). This is again confusing for several reasons. First, because they use the same unexplained decoding probability measure. Second, the optimal time point defined above depends on the start time of a stimulus, but here the start time is random. Third, the TDLM algorithm is hard to understand. For example, what are the reactivation probabilities of Figure 3C? They do make an effort to explain this in the methods section (lines 652-697) but it's not clear enough from the outset. For example, what does the state X_j is this a vector of activity of sensors? Are these decoding probabilities of the different directions? What is it? Also, what is X_i vs X_i(\Delta t)? Frankly, despite their efforts, I am very confused. Additionally, the figures use the term reactivation probability, where is it defined? So again, the results seem interesting, but the methods are not explained well at all.  

This paper must better explain the statistical methods so that they can be evaluated. This is not easy, these are relatively complex methods, but they must be explained much better so the validity of the paper can be examined.  

Regarding the optimal time point, we defined it as the time point with the highest decoding accuracy, determined during the validation of the localizer data using a leave-one-out cross-validation scheme. This optimal time point was participant- and motion-direction-specific, as the latency to achieve the peak decoding accuracy varied across individuals and motion directions. For group-level visualization, we circularly shifted the data over time, aligning each optimal time point to a common reference point (arbitrarily set at 200 ms after stimulus onset). Importantly, however, these time points are unrelated to the data in the main phase, as the models were trained using the independent localizer data and then applied to each time point during the blank period in the main phase.

Regarding the TDLM algorithm, detailed descriptions of the algorithm have been provided in the revised Methods section (Line 683 – 735). Furthermore, we have included explanatory notes in the main text and figure legend to provide immediate context for terms such as "reactivation probability" (Lines 247 – 248, Lines 275 – 276).

This paper uses MEG in humans, a non-invasive technique. This allows for such results in humans. Indeed (if the methods are correct) these units can be decoded to provide statistically significant estimates of motion direction. Note, however, that the spatial resolution of MEG is limited. The decoding accuracies of above 50% are way above chance. Note however that if actual motion-sensitive neurons (e.g. area MT) were recorded, and even if the motion is far from 100% coherence, the decoding accuracy would approach 100%. 

We agree with the reviewer that decoding accuracy would approach 100% if single-neuron data from motion-sensitive areas (e.g., area MT) were recorded, given the exceptionally high signal-to-noise ratio (SNR) of such data. However, two considerations inform the methodology of our study.

First, while single-neuron recordings provide invaluable insights, acquiring such data in humans is both ethically challenging and logistically impractical.

Non-invasive MEG, by contrast, offers a practical alternative that can achieve robust decoding of population-level activity with a reasonable SNR.

Second, the primary goal of our study was not merely to achieve high decoding accuracy but also to examine the replay of an exposed motion sequence in the human visual cortex. To achieve this, we first needed to train feature-specific models that can be used to decode the spontaneous reactivations of the four motion directions during the blank period. The ability to distinguish representations of the four motion directions was essential for calculating the “sequenceness” of the exposed motion sequence in the TDLM algorithm. While the absolute decoding accuracy of MEG data may not match that of single-neuron data, an important outcome was the successful construction of feature-specific models for the four motion directions (Figure 3B in the manuscript). These models provided a robust foundation for investigating sequential replay in the brain. These results also align with the broader goal of leveraging MEG data to study dynamic neural processes in humans, even in the face of its spatial resolution limitation.

Minor:  

(1) Line 246 - there is no figure S2A, subplots are not labeled.  

We have corrected this in the revised manuscript.

(2) Is Figure 3B referred to in the text? Same for 3C. This figure is there for explaining the statistical models used, but it is not well utilized.

We have modified the text to clarify this issue in the revised manuscript.

(3) English:  

There are problems with the use of English in the paper, this should be corrected in the next version. A few examples are below.  

Noises -> noise  

- "along the motion path in visual cortex" What does this sentence mean? Is this referring to motion-sensitive areas in the brain? Please clarify.  

There are many other examples. This is minor, but should be corrected.

We have corrected these errors in the revised manuscript.

References

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Ekman, M., Kusch, S., & de Lange, F. P. (2023). Successor-like representation guides the prediction of future events in human visual cortex and hippocampus. eLife, 12, e78904. https://doi.org/10.7554/eLife.78904

Gillespie, A. K., Maya, D. A. A., Denovellis, E. L., Liu, D. F., Kastner, D. B., Coulter, M. E., Roumis, D. K., Eden, U. T., & Frank, L. M. (2021). Hippocampal replay reflects specific past experiences rather than a plan for subsequent choice. Neuron, 109(19), 3149-3163.e6. https://doi.org/10.1016/j.neuron.2021.07.029

Gridchyn, I., Schoenenberger, P., O’Neill, J., & Csicsvari, J. (2020). AssemblySpecific Disruption of Hippocampal Replay Leads to Selective Memory Deficit. Neuron, 106(2), 291-300.e6. https://doi.org/10.1016/j.neuron.2020.01.021

Herrmann, B., Henry, M. J., Haegens, S., & Obleser, J. (2016). Temporal expectations and neural amplitude fluctuations in auditory cortex interactively influence perception. NeuroImage, 124, 487–497. https://doi.org/10.1016/j.neuroimage.2015.09.019

Igata, H., Ikegaya, Y., & Sasaki, T. (2021). Prioritized experience replays on a hippocampal predictive map for learning. Proceedings of the National Academy of Sciences, 118(1), e2011266118. https://doi.org/10.1073/pnas.2011266118

Lakatos, P., Karmos, G., Mehta, A. D., Ulbert, I., & Schroeder, C. E. (2008). Entrainment of Neuronal Oscillations as a Mechanism of Attentional Selection. Science, 320(5872), 110–113. https://doi.org/10.1126/science.1154735

Lakatos, P., Musacchia, G., O’Connel, M. N., Falchier, A. Y., Javitt, D. C., & Schroeder, C. E. (2013). The Spectrotemporal Filter Mechanism of Auditory Selective Attention. Neuron, 77(4), 750–761. https://doi.org/10.1016/j.neuron.2012.11.034

Liu, Y., Dolan, R. J., Kurth-Nelson, Z., & Behrens, T. E. J. (2019). Human Replay Spontaneously Reorganizes Experience. Cell, 178(3), 640-652.e14. https://doi.org/10.1016/j.cell.2019.06.012

Ólafsdóttir, H. F., Bush, D., & Barry, C. (2018). The Role of Hippocampal Replay in Memory and Planning. Current Biology, 28(1), R37–R50. https://doi.org/10.1016/j.cub.2017.10.073

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Overall I found the approach taken by the authors to be clear and convincing. It is striking that the conclusions are similar to those obtained in a recent study using a different computational approach (finite state controllers), and lends confidence to the conclusions about the existence of an optimal memory duration. There are a few questions that could be expanded on in future studies:

(1) Spatial encoding requirements

The manuscript contrasts the approach taken here (reinforcement learning in a gridworld) with strategies that involve a "spatial map" such as infotaxis. However, the gridworld navigation algorithm has an implicit allocentric representation, since movement can be in one of four allocentric directions (up, down, left, right), and wind direction is defined in these coordinates. Future studies might ask if an agent can learn the strategy without a known wind direction if it can only go left/right/forward/back/turn (in egocentric coordinates). In discussing possible algorithms, and the features of this one, it might be helpful to distinguish (1) those that rely only on egocentric computations (run and tumble), (2) those that rely on a single direction cue such as wind direction, (3) those that rely on allocentric representations of direction, and (4) those that rely on a full spatial map of the environment.

We agree that the question of what orientation skills are needed to implement an algorithm is interesting. We remark that our agents do not use allocentric directions in the sense of north, east, west and east relative to e.g. fixed landmarks in the environment. Instead, directions are defined relative to the mean wind, which is assumed fixed and known. (In our first answer to reviewers we used “north east south west relative to mean wind”, which may have caused confusion – but in the manuscript we only use upwind downwind and crosswind).

(2) Recovery strategy on losing the plume

The authors explore several recovery strategies upon losing the plume, including backtracking, circling, and learned strategies, finding that a learned strategy is optimal. As insects show a variety of recovery strategies that can depend on the model of locomotion, it would be interesting in the future to explore under which conditions various recovery strategies are optimal and whether they can predict the strategies of real animals in different environments.

Agreed, it will be interesting to study systematically the emergence of distinct recovery strategies and compare to living organisms.

(3) Is there a minimal representation of odor for efficient navigation?

The authors suggest that the number of olfactory states could potentially be reduced to reduce computational cost. They show that reducing the number of olfactory states to 1 dramatically reduces performance. In the future it would be interesting to identify optimal internal representations of odor for navigation and to compare these to those found in real olfactory systems. Does the optimal number of odor and void states depend on the spatial structure of the turbulence as explored in Figure 5?

We agree that minimal odor representations are an intriguing question. While tabular Q learning cannot derive optimal odor representations systematically, one could expand on the approach we have taken here and provide more comparisons. It will be interesting to follow this approach in a future study.

Reviewer #2 (Public review):

Summary:

The authors investigate the problem of olfactory search in turbulent environments using artificial agents trained using tabular Q-learning, a simple and interpretable reinforcement learning (RL) algorithm. The agents are trained solely on odor stimuli, without access to spatial information or prior knowledge about the odor plume's shape. This approach makes the emergent control strategy more biologically plausible for animals navigating exclusively using olfactory signals. The learned strategies show parallels to observed animal behaviors, such as upwind surging and crosswind casting. The approach generalizes well to different environments and effectively handles the intermittency of turbulent odors.

Strengths:

* The use of numerical simulations to generate realistic turbulent fluid dynamics sets this paper apart from studies that rely on idealized or static plumes.

* A key innovation is the introduction of a small set of interpretable olfactory states based on moving averages of odor intensity and sparsity, coupled with an adaptive temporal memory.

* The paper provides a thorough analysis of different recovery strategies when an agent loses the odor trail, offering insights into the trade-offs between various approaches.

* The authors provide a comprehensive performance analysis of their algorithm across a range of environments and recovery strategies, demonstrating the versatility of the approach.

* Finally, the authors list an interesting set of real-world experiments based on their findings, that might invite interest from experimentalists across multiple species.

Weaknesses:

* Using tabular Q-learning is both a strength and a limitation. It's simple and interpretable, making it easier to analyze the learned strategies, but the discrete action space seems somewhat unnatural. In real-world biological systems, actions (like movement) are continuous rather than discrete. Additionally, the ground-frame actions may not map naturally to how animals navigate odor plumes (e.g. insects often navigate based on their own egocentric frame).

We agree with the reviewer, and will look forward to study this problem further to make it suitable for meaningful comparisons with animal behavior.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have addressed my major concerns and I support publication of this interesting manuscript. A couple of small suggestions:

(1) In discussing performance in different environments (line 328-362) it might be easier to read if you referred to the environments by descriptive names rather than numbers.

Thank you for the suggestion, which we implemented

(2) Line 371: measurements of flow speed depend on antennae in insects. Insects can measure local speed and direct of flow using antennae, e.g. Bell and Kramer, 1979, Suver et al. 2019. Okubo et al. 2020,

Thank you for the references

(3) line 448: "Similarly, an odor detection elicits upwind surges that can last several seconds" maybe "Similarly, an odor detection elicits upwind surges that can outlast the odor by several seconds"?

Thank you for the suggestion

Reviewer #2 (Recommendations for the authors):

I commend the authors for their revisions in response to reviewer feedback.

While I appreciate that the manuscript is now accompanied by code and data, I must note that the accompanying code-repository lacks proper instructions for use and is likely incomplete (e.g. where is the main function one should run to run your simulations? How should one train? How should one recreate the results? Which data files go where?).

For examples of high-quality code-release, please see the documentation for these RL-for-neuroscience code repositories (from previously published papers):

https://github.com/ryzhang1/Inductive_bias

https://github.com/BruntonUWBio/plumetracknets

The accompanying data does provide snapshots from their turbulent plume simulations, which should be valuable for future research.

Thank you for the suggestions for how to improve clarity of the code. The way we designed the repository is to serve both the purpose of developing the code as well as sharing. This is because we are going to build up on this work to proceed further. Nothing is missing in the repository (we know it because it is what we actually use).

We do plan to create a more user-friendly version of the code, hopefully this will be ready in the next few months, but it wont be immediate as we are aiming to also integrate other aspects of the work we are currently doing in the Lab. The Brunton repository is very well organized, thanks for the pointer.

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

Reviewer #1 (Public review):

Overall I found the approach taken by the authors to be clear and convincing. It is striking that the conclusions are similar to those obtained in a recent study using a different computational approach (finite state controllers), and lend confidence to the conclusions about the existence of an optimal memory duration. There are a few points or questions that could be addressed in greater detail in a revision:

(1) Discussion of spatial encoding

The manuscript contrasts the approach taken here (reinforcement learning in a grid world) with strategies that involve a "spatial map" such as infotaxis. The authors note that their algorithm contains "no spatial information." However, I wonder if further degrees of spatial encoding might be delineated to better facilitate comparisons with biological navigation algorithms. For example, the gridworld navigation algorithm seems to have an implicit allocentric representation, since movement can be in one of four allocentric directions (up, down, left, right). I assume this is how the agent learns to move upwind in the absence of an explicit wind direction signal. However, not all biological organisms likely have this allocentric representation. Can the agent learn the strategy without wind direction if it can only go left/right/forward/back/turn (in egocentric coordinates)? In discussing possible algorithms, and the features of this one, it might be helpful to distinguish<br /> (1) those that rely only on egocentric computations (run and tumble),<br /> (2) those that rely on a single direction cue such as wind direction,<br /> (3) those that rely on allocentric representations of direction, and<br /> (4) those that rely on a full spatial map of the environment.

As Referee 1 points out, even if the algorithm does not require a map of space, the agent is still required to tell apart directions relative to the wind direction which is assumed known. Indeed, although in the manuscript we labeled actions allocentrically as “ up down left and right”, the source is always placed in the same location, hence “left” corresponds to upwind; “right” to downwind and “up” and “down” to crosswind right and left. Thus in fact directions are relative to the mean wind, which is therefore assumed known. We have better clarified the spatial encoding required to implement these strategies, and re-labeled the directions as upwind, downwind, crosswind-right and crosswind-left.

In reality, animals cannot measure the mean flow, but rather the local flow speed e.g. with antennas for insects, with whiskers for rodents and with the lateral line for marine organisms. Further work is needed to address how local flow measures enable navigation using Q learning.

(2) Recovery strategy on losing the plume

While the approach to encoding odor dynamics seems highly principled and reaches appealingly intuitive conclusions, the approach to modeling the recovery strategy seems to be more ad hoc. Early in the paper, the recovery strategy is defined to be path integration back to the point at which odor was lost, while later in the paper, the authors explore Brownian motion and a learned recovery based on multiple "void" states. Since the learned strategy works best, why not first consider learned strategies, and explore how lack of odor must be encoded or whether there is an optimal division of void states that leads to the best recovery strategies? Also, although the authors state that the learned recovery strategies resemble casting, only minimal data are shown to support this. A deeper statistical analysis of the learned recovery strategies would facilitate comparison to those observed in biology.

We thank Referee 1 for their remarks and suggestion to give the learned recovery a more prominent role and better characterize it. We agree that what is done in the void state is definitely key to turbulent navigation. In the revised manuscript, we have further substantiated the statistics of the learned recovery by repeating training 20 times and comparing the trajectories in the void (Figure 3 figure supplement 3, new Table 1). We believe however that starting with the heuristic recovery is clearer because it allows to introduce the concept of recovery more clearly. Indeed, the learned “recovery” is so flexible that it ends up mixing recovery (crosswind motion) to aspects of exploitation (surge): we defer a more in-depth analysis that disentangles these two aspects elsewhere. Also, we added a whole new comparison with other biologically inspired recoveries both in the native environment and for generalization (Figure 3 and 5).

(3) Is there a minimal representation of odor for efficient navigation?

The authors suggest (line 280) that the number of olfactory states could potentially be reduced to reduce computational cost. This raises the question of whether there is a maximally efficient representation of odors and blanks sufficient for effective navigation. The authors choose to represent odor by 15 states that allow the agent to discriminate different spatial regimes of the stimulus, and later introduce additional void states that allow the agent to learn a recovery strategy. Can the number of states be reduced or does this lead to loss of performance? Does the optimal number of odor and void states depend on the spatial structure of the turbulence as explored in Figure 5?

We thank the referee for their comment. Q learning defines the olfactory states prior to training and does not allow a systematic optimization of odor representation for the task. We can however compare different definitions of the olfactory states, for example based on the same features but different discretizations. We added a comparison with a drastically reduced number of non-empty olfactory states to just 1, i.e. if the odor is above threshold at any time within the memory, the agent is in the non-void olfactory state, otherwise it is in the void state. This drastic reduction in the number of olfactory states results in less positional information and degrades performance (Figure 5 figure supplement 5).

The number of void states is already minimal: we chose 50 void states because this matches the time agents typically remain in the void (less than 50 void states results in no convergence and more than 50 introduces states that are rarely visited).

One may instead resort to deep Q-learning or to recurrent neural networks, which however do not provide answers as for what are the features or olfactory states that drive behavior (see discussion in manuscript and questions below).

Reviewer #2 (Public review):

Summary:

The authors investigate the problem of olfactory search in turbulent environments using artificial agents trained using tabular Q-learning, a simple and interpretable reinforcement learning (RL) algorithm. The agents are trained solely on odor stimuli, without access to spatial information or prior knowledge about the odor plume's shape. This approach makes the emergent control strategy more biologically plausible for animals navigating exclusively using olfactory signals. The learned strategies show parallels to observed animal behaviors, such as upwind surging and crosswind casting. The approach generalizes well to different environments and effectively handles the intermittency of turbulent odors.

Strengths:

(1) The use of numerical simulations to generate realistic turbulent fluid dynamics sets this paper apart from studies that rely on idealized or static plumes.

(2) A key innovation is the introduction of a small set of interpretable olfactory states based on moving averages of odor intensity and sparsity, coupled with an adaptive temporal memory.

(3) The paper provides a thorough analysis of different recovery strategies when an agent loses the odor trail, offering insights into the trade-offs between various approaches.

(4) The authors provide a comprehensive performance analysis of their algorithm across a range of environments and recovery strategies, demonstrating the versatility of the approach.

(5) Finally, the authors list an interesting set of real-world experiments based on their findings, that might invite interest from experimentalists across multiple species.

Weaknesses:

(1) The inclusion of Brownian motion as a recovery strategy, seems odd since it doesn't closely match natural animal behavior, where circling (e.g. flies) or zigzagging (ants' "sector search") could have been more realistic.

We agree that Brownian motion may not be biologically plausible -- we used it as a simple benchmark. We clarified this point, and re-trained our algorithm with adaptive memory using circling and zigzaging (cast and surge) recoveries. The learned recovery outperforms all heuristic recoveries (Figure 3D, metrics G). Circling ranks second, and achieves these good results by further decreasing the probability of failure and paying slightly in speed. When tested in the non-native environments 2 to 6, the learned recovery performs best in environments 2, 5 and 6 i.e. from long range more relevant to flying insects; whereas circling generalizes best in odor rich environments 3 and 4, representative of closer range and close to the substrate (Figure 5B, metrics G). In the new environments, similar to the native environment, circling favors convergence (Figure 5B, metrics f⁺) over speed (Figure 5B, metrics g⁺ and τ_min/τ), which is particularly deleterious at large distance.

(2) Using tabular Q-learning is both a strength and a limitation. It's simple and interpretable, making it easier to analyze the learned strategies, but the discrete action space seems somewhat unnatural. In real-world biological systems, actions (like movement) are continuous rather than discrete. Additionally, the ground-frame actions may not map naturally to how animals navigate odor plumes (e.g. insects often navigate based on their own egocentric frame).

We agree with the reviewer that animal locomotion does not look like a series of discrete displacements on a checkerboard. However, to overcome this limitation, one has to first focus on a specific system to define actions in a way that best adheres to a species’ motor controls. Moreover, these actions are likely continuous, which makes reinforcement learning notoriously more complex. While we agree that more realistic models are definitely needed for a comparison with real systems, this remains outside the scope of the current work. We have added a remark to clarify this limitation.

(3) The lack of accompanying code is a major drawback since nowadays open access to data and code is becoming a standard in computational research. Given that the turbulent fluid simulation is a key element that differentiates this paper, the absence of simulation and analysis code limits the study's reproducibility.

We have published the code and the datasets at

- code: https://github.com/Akatsuki96/qNav

- datasets: https://zenodo.org/records/14655992

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Line 59-69: In comparing the results here to other approaches (especially the Verano and Singh papers), it would also be helpful to clarify which of these include an explicit representation of the wind direction. My understanding is that both the Singh and Verano approaches include an explicit representation of wind direction. In Singh wind direction is one of the observations that inputs to the agent, while in Verano, the actions are defined relative to the wind direction. In the current paper, my understanding is that there is no explicitly defined wind direction, but because movement directions are encoded allocentrically, the agent is able to learn the upwind direction from the structure of the plume- is this correct? I think this information would be helpful to spell out and also to address whether an agent without any allocentric direction sense can learn the task.

Thank you for the comment. In our algorithm the directions are defined relative to the mean wind, which is assumed known, as in Verano et al. As far as we understand, Singh et al provide the instantaneous, egocentric wind velocities as part of the input.

(1) Line 105: "several properties of odor stimuli depend on the distance from the source" might cite Boie...Victor 2018, Ackles...Schaefer, 2021, Nag...van Breugel 2024.

Thank you for the suggestions - we have added these references

(2) Line 130: "we first define a finite set of olfactory states" might be helpful to the reader to state what you chose in this paragraph rather than further down.

We have slightly modified the incipit of the paragraph. We first declare we are setting out to craft the olfactory states, then define the challenges, finally we define the olfactory states.

(3) Line 267: "Note that the learned recovery strategy resembles casting behavior observed in flying insects" Might note that insects seem to deploy a range of recovery strategies depending on locomotor mode and environment. For example, flying flies circle and sink when odor is lost in windless environments (Stupski and van Breugel 2024).

Thank you for your comment. We have included the reference and we now added comparisons to results using circling and cast & surge recovery strategies.

(4) Line 289: "from positions beyond the source, the learned strategy is unable to recover the plume as it mostly casts sideways, with little to no downwind action" This is curious as many insects show a downwind bias in the absence of odor that helps them locate the plumes in the first place (e.g. Wolf and Wehner, 2000, Alvarez-Salvado et al. 2018). Is it possible that the agent could learn a downwind bias in the absence of odor if given larger environments or a longer time to learn?

The reviewer is absolutely correct – Downwind motion is not observed in the recovery simply because the agent rarely overshoots the source. Hence overall optimization for that condition is washed out by the statistics. We believe downwind motion will emerge if an agent needs to avoid overshooting the source – we do not have conclusive results yet but are planning to introduce such flexibility in a further work. We added this remark and refs.

(5) Line 377-391: testing these ideas in living systems. Interestingly, Kathman..Nagel 2024 (bioRxiv) shows exactly the property predicted here and in Verano in fruit flies- an odor memory that outlasts the stimulus by a duration of several seconds, appropriate for filling in "blanks." Relatedly, Alvarez-Salvado et al. 2018 showed that fly upwind running reflected a temporal integration of odor information over ~10s, sufficient to avoid responding to blanks as loss of odor.

Indeed, we believe this is the most direct connection between algorithms and experiments. We are excited to discuss with our colleagues and pursue a more direct comparison with animal behavior. We were aware of the references and forgot to cite them, thank you for your careful reading of our work !

Reviewer #2 (Recommendations for the authors):

Suggestions

(1) The paper does not clearly specify which type of animals (e.g., flying insects, terrestrial mammals) the model is meant to approximate or not approximate. The authors should consider clarifying how these simulations are suited to be a general model across varied olfactory navigators. Further, it isn't clear how low/high the intermittency studied in this model is compared to what different animals actually encounter. (Minor: The Figure 4 occupancy circles visualization could be simplified).

Environment 1 represents the lower layers of a moderately turbulent boundary layer. Search occurs on a horizontal plane ~half meter from the ground. The agent is trained at distances of about 10 meters and also tested on longer distances  ~ 17 meters (environment 6), lower heights ~1cm from the ground (environments 3-4), lower Reynolds number (environment 5) and higher threshold of detection (environment 2 and 4). Thus Environments 1,2,5 and 6 are representative of conditions encountered by flying organisms (or pelagic in water), and Environments 3 and 4 of searches near the substrate, potentially involved in terrestrial navigation (benthic in water). Even near the substrate, we use odor dispersed in the fluid, and not odor attached to the substrate (relevant to trail tracking).

Also note that we pick Schmidt number Sc = 1 and this is appropriate for odors in air but not in water. However, we expect a weak dependence on the Schmidt number as the Batchelor and Kolmogorov scales are below the size of the source and we are interested in the large scale statistics Falkovich et al., 2001; Celani et al., 2014; Duplat et al., 2010.

Intermittency contours are shown in Fig 1C, they are highest along the centerline, and decay away from the centerline, so that even within the plume detecting odor is relatively rare. Only a thin region near the centerline has intermittency larger than 66%; the outer and most critical bin of the plume has intermittency under 33%; in the furthest point on the centerline intermittency is <10%. For reference, experimental values in the atmospheric boundary layer report intermittency 25% to 20% at 2 to 15m from the source along the centerline (Murlis and Jones, 1981).

We have more clearly labeled the contours in Fig 1C and added these remarks.

We included these remarks and added a whole table with matching to real conditions within the different environments.

(2) Could some biological examples and references be added to support that backtracking is a biologically plausible mechanism?

Backtracking was observed e.g. in ants displaced in unfamiliar environments (Wystrach et al, P Roy Soc B, 280,  2013), in tsetse flies executing reverse turns uncorrelated to wind, which bring them back towards the location where they last detected odor (Torr, Phys Entom, 13, 1988, Gibson & Brady Phys Entom 10, 1985) and in coackroaches upon loss of contact with the plume (Willis et al, J. Exp. Biol. 211, 2008). It is also used in computational models of olfactory navigation (Park et al, Plos Comput Biol, 12:e1004682, 2016).

(3) Hand-crafted features can be both a strength and a limitation. On the one hand, they offer interpretability, which is crucial when trying to model biological systems. On the other hand, they may limit the generality of the model. A more thorough discussion of this paper's limitations should address this.

(4) The authors mention the possibility of feature engineering or using recurrent neural networks, but a more concrete discussion of these alternatives and their potential advantages/disadvantages would be beneficial. It should be noted that the hand-engineered features in this manuscript are quite similar to what the model of Singh et al suggests emerges in their trained RNNs.

Merged answer to points 3 and 4.

We agree with the reviewer that hand-crafted features are both a strength and a limitation in terms of performance and generality. This was a deliberate choice aimed at stripping the algorithm bare of implicit components, both in terms of features and in terms of memory. Even with these simple features, our model performs well in navigating across different signals, consistent with our previous results showing that these features are a “good” surrogate for positional information.

To search for the most effective temporal features, one may consider a more systematic hand crafting, scaling up our approach. In this case one would first define many features of the odor trace; rank groups of features for their accuracy in regression against distance; train Q learning with the most promising group of features and rank again. Note however that this approach will be cumbersome because multiple factors will have to be systematically varied: the regression algorithm; the discretization of the features and the memory.

Alternatively, to eliminate hand crafting altogether and seek better performance or generalization, one may consider replacing these hand-crafted features and the tabular Q-learning approach with recurrent neural networks or with finite state controllers. On the flip side, neither of these algorithms will directly provide the most effective features or the best memory, because these properties are hidden within the parameters that are optimized for. So extra work is needed to interrogate the algorithms and extract these information. For example, in Singh et al, the principal components of the hidden states in trained agents correlate with head direction, odor concentration and time since last odor encounter. More work is needed to move beyond correlations and establish more systematically what are the features that drive behavior in the RNN.

We have added these points to the discussion.

(5) Minor: the title of the paper doesn't immediately signal its focus on recovery strategies and their interplay with memory in the context of olfactory navigation. Given the many other papers using a similar RL approach, this might help the authors position this paper better.

We agree with the referee and have modified the title to reflect this.

(6) Minor: L 331: "because turbulent odor plumes constantly switch on and off" -- the signal received rather than the plume itself is switching on and off.

Thank you for the suggestion, we implemented it.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this elegant and thorough study, Sánchez-León et al. investigate the effects of tDCS on the firing of single cerebellar neurons in awake and anesthetized mice. They find heterogeneous responses depending on the orientation of the recorded Purkinje cell.

Strengths:

The paper is important in that it may well explain part of the controversial and ambiguous outcomes of various clinical trials. It is a well-written paper on a deeply analyzed dataset.

We sincerely thank Reviewer #1 for their positive feedback and insightful comments. We are pleased to know that you found our study elegant and thorough, and we appreciate your recognition of its potential to clarify the controversial and ambiguous outcomes seen in various clinical trials. Your acknowledgment of the depth of our analysis and the clarity of the writing is highly encouraging, and we are grateful for your thoughtful evaluation of our work.

Weaknesses:

The sample size could be increased for some of the experiments.

We sincerely thank the reviewer for their thoughtful suggestion to increase the sample size. While we understand the importance of this consideration, we believe it is not feasible at this stage due to several factors. First, the complexity of our experiments, which include single-neuron recordings in awake animals during electric field application, juxtacellular neurobiotin injections post-tDCS (with a low success rate), and high-density recordings from Purkinje cells across different layers in awake animals, significantly limits the throughput of data collection. Second, the statistical outcomes obtained from our analyses, which combine multiple techniques, are robust and provide a strong basis for our conclusions. Third, the current study already involves a substantial number of animals (74 mice), which aligns with ethical considerations for minimizing animal use while ensuring robust results.

We believe that the current sample size is sufficient to support the findings presented in the manuscript. Expanding the sample size further would require considerable additional resources and time, without a clear indication that it would fundamentally alter the conclusions of the study. We are grateful for the reviewer’s understanding of these limitations and their acknowledgment of the value of the current dataset.

Reviewer #2 (Public review):

Summary:

In this study by Sánchez-León and colleagues, the authors attempted to determine the influence of neuronal orientation on the efficacy of cerebellar tDCS in modulating neural activity. To do this, the authors made recordings from Purkinje cells, the primary output neurons of the cerebellar cortex, and determined the inter-dependency between the orientation of these cells and the changes in their firing rate during cerebellar tDCS application.

Strengths:

(1) A major strength is the in vivo nature of this study. Being able to simultaneously record neural activity and apply exogenous electrical current to the brain during both an anesthetized state and during wakefulness in these animals provides important insight into the physiological underpinnings of tDCS.

(2) The authors provide evidence that tDCS can modulate neural activity in multiple cell types.

For example, there is a similar pattern of modulation in Purkinje cells and non-Purkinje cells (excitatory and inhibitory interneurons). Together, these data provide wholistic insight into how tDCS can affect activity across different populations of cells, which has important implications for basic neuroscience, but also clinical populations where there may be non-uniform or staged effects of neurological disease on these various cell types.

(3) There is a systematic investigation into the effects of tDCS on neural activity across multiple regions of the cerebellum. The authors demonstrate that the pattern of modulation is dependent on the target region. These findings have important implications for determining the expected neuromodulatory effects of tDCS when applying this technique over different target regions noninvasively in animals and humans.

We sincerely thank Reviewer #2 for their detailed and thoughtful comments on our study. We are pleased that you recognized the importance of our in vivo approach, allowing for simultaneous neural recordings and tDCS application in both anesthetized and awake states. Your acknowledgment of our findings regarding the modulation of neural activity across different cell types, including Purkinje and non-Purkinje cells, is greatly appreciated. We also value your recognition of the implications of our work for understanding how tDCS can affect diverse neuronal populations, particularly in the context of clinical applications. Additionally, your positive feedback on our systematic investigation across multiple cerebellar regions highlights the relevance of our work for determining the region-specific effects of tDCS. Thank you for your encouraging and insightful evaluation.

Weaknesses:

(1) In the introduction, there is a lack of context regarding why neuronal orientation might be a critical factor influencing the responsiveness to tDCS. The authors allude to in vitro studies that have shown neuronal orientation to be relevant for the effects of tDCS on neural activity but do not expand on why this might be the case. These points could be better understood by informing the reader about the uniformity/non-uniformity of the induced electric field by tDCS. In addition, there is a lack of an a priori hypothesis. For example, would the authors have expected that neuronal orientation parallel or perpendicular to the electrical field to be related to the effects of tDCS on neural activity?

We thank the Reviewer #2 for this insightful comment. In response, we have expanded the introduction to provide a clearer context regarding the influence of neuronal orientation on the effects of tDCS. Therefore, we have added two new paragraphs in the Introduction to address these points.

“For neurons whose somatodendritic axis is aligned with the electric field, the field induces a pronounced somatic polarization. In the case of anodal stimulation, where the positive electrode is positioned near the dendrites and the soma is oriented away, positively charged ions accumulate near the soma, leading to depolarization and increased excitability, thus facilitating action potential generation. Conversely, neurons whose orientation opposes the field, such as when the soma is closer to the positive electrode and the dendrites face away, experience hyperpolarization, reducing excitability. Lastly, neurons oriented perpendicular to the electric field would exhibit minimal somatic polarization, as the field does not induce significant redistribution of charges along the somatodendritic axis.”

Additionally, we have now clarified our a priori hypothesis regarding neuronal orientation and its expected influence on tDCS efficacy.

“We hypothesized that the orientation of PCs relative to the electric field would influence the effects of tDCS on neural activity. In the Vermis, PCs oriented parallel to the field are expected to exhibit stronger effects due to greater somatic polarization, leading to depolarization or hyperpolarization depending on the orientation of the somatodendritic axis. Conversely, PCs in Crus I/II, which are oriented obliquely to the field, are expected to exhibit intermediate effects, as the oblique alignment reduces the strength of polarization compared to parallel alignment.”

(2) It is unclear how specific stimulation parameters were determined. First, how were the tDCS intensities used in the present experiments determined/selected, and how does the relative strength of this induced electric field equate to the intensities used non-invasively during tDCS experiments in humans? Second, there is also a fundamental difference in the pattern of application used here (e.g., 15 s pulses separated by 10 s of no stimulation) compared to human studies (e.g., 10-20 min of constant stimulation).

We thank Reviewer #2 for their observations. We proceed to address their concerns and included the following text in the main manuscript, Discussion section: 

“We used higher values than those applied in human experiments to achieve more reliable results. As seen in Supplementary Fig. 3, neurons are modulated in a similar way for 100, 200 or 300 µA but higher intensities elicited significant changes in a greater proportion of these neurons. In addition, a previous study from our lab23 using the same methodology, showed that 100, 200 and 300 µA (eliciting from 5.9 to 125.7 V/m in the current study) were ideal to obtain reliable and robust results in neuronal modulation, while keeping animal awareness of the stimulation at a minimum level. Besides, Asan et al. has recently shown that using epidural stimulation in anesthetized rats under an electric field closer to human studies (1.5–7.5 V/m) was also able to modulate the activity of cerebellar neurons.”

In addition, we add the following text to the Results section under ‘tDCS modulates Purkinje cell activity in awake mice in a heterogeneous manner’ section:

“This protocol allows us to avoid the development of plasticity effects, which are known to require at least several minutes of tDCS administration, and to test the direct electrical modulation exerted by the externally applied currents.”

(3) In their first experiment, the authors measure the electric field strength at increasing depths during increasing stimulation intensities. However, it appears that an alternating current rather than a direct current, which is usually employed in tDCS protocols, was used. There is a lack of rationale regarding why the alternating current was used for this component. Typically, this technique is more commonly used for entraining/boosting neural oscillations compared to studies using tDCS which aim to increase or decrease neural activity in general.

We appreciate Reviewer #2’s assessment of the differences between tDCS and tACS. We will clarify this distinction. We chose tACS for measuring electric field strength for two main reasons:

• Amplifier Limitations: The amplifiers commonly used in electrophysiology are designed to filter out low-frequency components, including direct current (DC) signals, using a highpass filter. This is due to the fact that the neuronal signals of interest, such as action potentials, typically occur at higher frequencies (several Hz to kHz). Consequently, any DC signal applied is filtered out from the recordings, preventing us from measuring changes in voltage effectively.

• Impedance Changes: DC stimulation can alter the impedance of electrodes and surrounding tissue over time. To mitigate this effect and maintain stable recordings, it is advantageous to frequently alternate the polarity and intensity of the stimulation.

This next text has been included in the 'Transcranial Electrical Stimulation' section of the 'Materials and Methods' part of the manuscript:

“We selected tACS to measure electric field strength due to two main reasons: (1) amplifiers used in electrophysiology filter out low-frequency signals like DC, making voltage changes from tDCS undetectable, and (2) DC stimulation can alter electrode and tissue impedance over time, whereas alternating the polarity in tACS helps maintain stable recordings.”

It is important to note that our aim with tACS is to provide an approximation of current propagation through the tissue, rather than to exactly replicate the baseline conditions encountered during continuous tDCS stimulation.

Reviewer #3 (Public review):

Summary:

In this study, Sanchez-Leon et al. combined extracellular recordings of Purkinje cell activity in awake and anesthetized mice with juxtacellular recordings and Purkinje cell staining to link Purkinje cell orientation to their stimulation response. The authors find a relationship between neuron orientation and firing rate, dependent on stimulation type (anodal/cathodal). They also show the effects of stimulation intensity and rebound effects.

Strengths:

Overall, the work is methodologically sound and the manuscript is well written. The authors have taken great care to explain their rationale and methodological choices.

We sincerely thank Reviewer #3 for their positive feedback and constructive comments regarding our study. We are pleased that you found our work methodologically sound and well written. Your acknowledgment of our efforts to explain our rationale and methodological choices is greatly appreciated. We believe that the insights gained from linking Purkinje cell orientation to their stimulation response will contribute significantly to our understanding of cerebellar function and tDCS effects. Thank you for your thoughtful evaluation of our manuscript.

Weaknesses:

My only reservation is the lack of reporting of the precise test statistics, p-values, and multiple comparison corrections. The work would benefit from adding this and other information.

We sincerely thank Reviewer #3 for their valuable feedback and for highlighting an important aspect of our analysis. We agree that the inclusion of precise test statistics, p-values, and details on multiple comparison corrections would strengthen the robustness of our findings. In response to your suggestion, we have now added this information to the Results section, ensuring that all statistical tests, exact p-values, and corrections for multiple comparisons are clearly reported. We believe these additions provide greater transparency and rigor to our analysis, and we appreciate your thoughtful recommendation.

Major Comments:

(1) The authors should report the exact test statistics. These are missing for all comparisons and hinder the reader from understanding what exactly was tested for each of the experiments. For example, having the exact test statistics would help better understand the non-significant differences in Figure 1h where there is at least a numeric difference in CS firing rate during tDCS.

As mentioned before, we have now included the precise test statistics for all statistical comparisons throughout the manuscript. Specifically, in the case of Supplementary Figure 1h, we have added the exact values for the comparisons of CS firing rates during tDCS, even for nonsignificant differences, to ensure transparency and to clarify the observed numerical differences. We believe these additions will help readers better interpret the data and understand the statistical underpinnings of our findings. 

However, given the large amount of data analyzed, particularly related to individual neuronal activity, it is not feasible to present all of the data for each individual neuron. We have aimed to provide a comprehensive statistical summary without overwhelming the reader with an excessive amount of detailed data.

(2) Did the authors apply any corrections for multiple comparisons? Generally, it would be helpful if they could clarify the statistical analysis (which values were subjected to the tests, how many tests were performed for each question, etc.).

We appreciate the reviewer’s comment regarding the need for clarification on the statistical analysis and the application of multiple comparison corrections. In response, we have updated the main text to include all the requested information. Specifically, we have added the appropriate multiple comparison tests (Tukey's or Nemenyi) where applicable to each analysis. These corrections have been applied to ensure that the results are robust and account for the number of comparisons made. We have also clarified the specific tests used for each analysis, the values subjected to these tests, and the number of comparisons performed for each question. This information is now detailed in the Methods section under 'Statistical Analysis' for transparency and to aid in the interpretation of the results.

(3) The relationship shown in Figure 2g seems to be influenced by the two outliers. Have the authors confirmed the results using a robust linear regression method?

We agree with the reviewer that the two neurons in Figure 2g could appear as outliers. To address this, we applied the ROUT method with a stringent Q = 1% to detect potential outliers, and none were found. In addition, we have confirmed the robustness of our results by performing a complementary analysis using robust linear regression methods (e.g., M-estimators), which showed consistent findings with our original analysis. For this purpose, we used the 'Huber' loss function, which combines least squares with robustness against outliers. The regression line obtained with this method (y = -0.5650x + 157.4556) differs minimally from the originally presented value, with the p-value of the slope and the intercept being p = 1.4846x10^-4 (t₍₂₂₎ = -4.5740) and p = 1.1382x10^-11 (t₍₂₂₎ \= 12.8010), respectively. Author response image 1 shows both regression fits to facilitate their comparison. These additional steps ensure the reliability of the relationship observed in the figure, even when accounting for the potential influence of the two data points.

Author response image 1.

(4) The authors conclude that tDCS modulates vermal PCs more than Crus I/II PCs - but they don't seem to test this statistically. It would be helpful to submit the firing rate change values to an actual statistical test to conclude this directly from the data.

We agree that it would be appropriate to apply a statistical test to determine whether there is similarity in the level of modulation. To this end, we have normalized the modulation so that all data are positive. For example, a neuron that increases or decreases its activity by 50% relative to the baseline period will be considered as having a modulation of 50% in both cases. This yields a mean modulation of 9.42% for neurons recorded in Crus I/II and 62.35% for those in the Vermis. Since the two distributions do not meet the normality assumption (Shapiro-Wilk test), we used a Mann-Whitney test, which resulted in a p-value < 0.0001, thus demonstrating a significant difference in modulation between the two cerebellar regions analyzed. We added this information to the main text. Additionally, we included a new panel in Supplementary Figure 3 (Supplementary Figure 3i) to visually represent these data.

Reviewer #1 (Recommendations for the authors):

I have several suggestions to further improve the paper:

(1) It remains unclear how many tDCS trials were done during each single-cell recording. What were the inclusion criteria? Were tens of trials done per cell or was a cell already included if the recording was stable during a few trials? Please clarify.

For every single-cell recording, the maximum number of trials allowed by the recording stability were applied. A neuron was included in the analysis if the recording was stable for at least 2 trials at a given intensity and polarity, and up to a maximum of 1 hour recording. We introduced a paragraph in the methods section explaining this.

(2) Along the same line, could the authors show cell responses to individual consecutive trials? Do the responses change over time? For example, does a cell increase the firing rate more during early trials compared to late trials? Please clarify.

We appreciate the reviewer’s suggestion to investigate whether cell responses change over consecutive trials. In our data, when tDCS effects were observed, the changes in firing rate were evident from the very first trials in some neurons. To illustrate this, we have included Author response image 2, which shows examples of individual neuron responses (2 non-PC on the left and 2 PC on the right) across consecutive trials. Red and blue histogram bars indicate anodal and cathodal tDCS periods, respectively.

Author response image 2.

However, a rigorous analysis of the stimulation effect over time across trials was not feasible due to the considerable variability in the number of trials applied to different recorded neurons. This variability arose from differences in the duration for which stable recordings could be maintained.

Despite this limitation, the early responses to tDCS provide valuable insights into the immediate effects of stimulation on neuronal activity.

(3) Neurons are recorded very superficially, just below a 2 mm wide craniotomy. The temperature of the brain is likely lower than a normal physiological temperature. Did the authors consider the potential effects of temperature? Please address.

We acknowledge the reviewer's concern regarding the potential effects of temperature on the recorded neurons. While it is challenging to precisely control the temperature of the tissue in the recording area, it is important to note that the temperature conditions were consistent across both the control and stimulation phases of the experiment. This consistency ensures that any potential effects of temperature are evenly distributed across conditions, thereby minimizing its impact on the observed changes in neuronal activity. Furthermore, although the recordings are conducted 2 mm below the craniotomy, this region is continuously bathed in saline, with an additional 3 mm of fluid maintained at physiological temperature, effectively preventing dehydration and cooling of the surface tissue. 

(4) More general, but along the same line, is there any effect of the depth of the recorded cells on its response to stimulations for any of the data collected in this study? Figure 1 nicely shows that there is a significant electric field at depths up to 4 mm, but do more superficial cells have stronger/weaker responses to cathodal/anodal stimulation, as the electric field there is much stronger?

We were also expecting to see some correlation between depth and degree of modulation, however, a linear regression analysis showed very low R² values (see Author response images 3-6), suggesting a negligible correlation between depth of recording and neuronal activity modulation. We did this analysis for Purkinje and non-Purkinje cells separately, as well as for recordings in CrusI-II or Vermis, showing similar negative results in all cases.

Author response image 3.

Author response table 1.

Author response image 4.

Author response table 2.

Author response image 5.

Author response table 3.

Author response image 6.

Author response table 4.

(5) The authors are recording the movements of the mouse on a treadmill. Was there any correlation between tDCS and behavior? And between behavior and firing patterns? Please address.

We appreciate the reviewer’s question regarding the potential correlation between tDCS and behavior, as well as between behavior and firing patterns. In our experimental setup, the movement of the mouse typically introduces electrical artifacts in the recordings, particularly during running on the treadmill. To ensure the accuracy of our data, trials that coincided with running or other significant movements were excluded from the analysis. This is explained in the Methods section of the main text under 'Data analysis' within the description of how single-cell activity was processed. On the other hand, conscious of the modulatory effects that animal movement or specific behaviors may have on neuronal firing rates, we thought that trials involving movement should be eliminated to avoid any potential confounding with the effects of current application. 

(6) The strength of the electrical field seems highly variable. Do the authors have an explanation for this? Please address.

We appreciate the reviewer’s observation regarding the variability in the strength of the electric field. This variability is indeed expected, given the inherent inter-individual differences in skull thickness across animals (which, as discussed in the main manuscript, attenuates around 20% of the current), as well as slight variations in the precise placement of the tES active electrode during surgery. These factors can lead to fluctuations in the electric field, although they remain within the same order of magnitude.

(7) As the authors stated, even for cells recorded at a depth of over 2 mm, the electric fields are still much higher than the fields generated in human studies. Why were there no comparable strengths used? Please address.

We thank the reviewer for raising this important point. Previous studies from our lab (SánchezLeón et al. 2021) demonstrated minimal modulation in neuronal activity (LFP) when using tDCS intensities below 200 µA in awake animals. To achieve stronger and more consistent effects, we selected an intensity of 200 µA for our experiments. It is well-established that small animals, such as mice, require higher electric field strengths than humans to induce observable effects (Ozen et al., 2010; Vöröslakos et al., 2018; Asan et al., 2020). This discrepancy may be attributed to several factors, including differences in neuronal density within the stimulated networks (Herculano-Houzel et al., 2009), as well as variations in axonal length and diameter (Chakraborty et al., 2018). However, as we stated in the Discussion, we also found modulated neurons for electric fields close to those in humans:

“Importantly, we observe clear firing rate modulation of PCs and non-PCs at depths of 2.3 mm and tDCS intensity of 100 μA, where the measured electric field is as low as 5.9 V/m.”

Despite these limitations, animal models remain invaluable for obtaining high-resolution invasive data that cannot be collected in human studies. Such experiments are crucial for understanding the basic mechanisms underlying non-invasive brain stimulation, validating computational models, and exploring the therapeutic potential of these techniques for various neurological conditions.

References:

Asan, A. S., Lang, E. J., & Sahin, M. (2020). Entrainment of cerebellar purkinje cells with directional AC electric fields in anesthetized rats. Brain stimulation, 13(6), 1548–1558. https://doi.org/10.1016/j.brs.2020.08.017 

Chakraborty, D., Truong, D. Q., Bikson, M., & Kaphzan, H. (2018). Neuromodulation of Axon Terminals. Cerebral cortex (New York, N.Y. : 1991), 28(8), 2786–2794. https://doi.org/10.1093/cercor/bhx158

Herculano-Houzel S. (2009). The human brain in numbers: a linearly scaled-up primate brain. Frontiers in human neuroscience, 3, 31. https://doi.org/10.3389/neuro.09.031.2009

Ozen, S., Sirota, A., Belluscio, M. A., Anastassiou, C. A., Stark, E., Koch, C., & Buzsáki, G. (2010). Transcranial electric stimulation entrains cortical neuronal populations in rats. The Journal of neuroscience : the official journal of the Society for Neuroscience, 30(34), 11476–11485. https://doi.org/10.1523/JNEUROSCI.5252-09.2010

Vöröslakos, M., Takeuchi, Y., Brinyiczki, K., Zombori, T., Oliva, A., Fernández-Ruiz, A., Kozák, G., Kincses, Z. T., Iványi, B., Buzsáki, G., & Berényi, A. (2018). Direct effects of transcranial electric stimulation on brain circuits in rats and humans. Nature communications, 9(1), 483. https://doi.org/10.1038/s41467-018-02928-3

(8) It seems that there is a very high number of mice used for a relatively small number of cellular recordings. Can the authors explain this?

We appreciate the reviewer’s observation regarding the number of mice used relative to the number of recorded neurons. There are several factors contributing to this:

(1)  In vivo juxtacellular labeling is a complex, multi-step process where each step must be executed precisely to successfully label a neuron. During blind recordings, it is impossible to ensure with 100% certainty that the neuron targeted for juxtacellular labeling will later be recoverable with sufficient staining (Pinault, 1996). To maintain confidence in the correspondence between the recorded and labeled neuron, we typically limit our attempts to label one neuron per mouse, or at most, two neurons located far apart from each other.

(2)  Recording duration limitations: The probability of maintaining a well-isolated, stable neuronal recording decreases significantly as the recording time increases. To obtain sufficient data with multiple tDCS trials, it is necessary to conduct numerous independent recordings. Additionally, each time the recording pipette penetrates the recording site, there is a minor but cumulative impact on the dura mater and neural tissue, leading to tissue degradation in subsequent recordings.

(3)  Diverse experimental conditions: This study explores several conditions, including recordings in anesthetized and awake mice, targeting different cerebellar regions (Crus I/II and vermis), and utilizing a range of techniques (single-unit extracellular recordings using glass pipettes, juxtacellular recording and labeling, and high-density recordings using the Neuropixels system). These distinct approaches required the establishment of independent experimental animal groups, which contributed to the higher number of subjects used in the study.

Although we were often able to record several neurons per mouse, the final number of neurons that met all criteria for analysis was reduced due to these limitations.

References:

Pinault D. (1996). A novel single-cell staining procedure performed in vivo under electrophysiological control: morpho-functional features of juxtacellularly labeled thalamic cells and other central neurons with biocytin or Neurobiotin. Journal of neuroscience methods, 65(2), 113–136. https://doi.org/10.1016/0165-0270(95)00144-1

(9) The N for both the neurobiotin-stained neurons and the Neuropixels recordings was relatively low. If possible, it would be nice to see a few more cells.

We sincerely thank the reviewer for their thoughtful suggestion to increase the sample size. While we understand the importance of this consideration, we believe it is not feasible at this stage due to several factors. First, the complexity of our experiments, which include single-neuron recordings in awake animals during electric field application, juxtacellular neurobiotin injections post-tDCS (with a low success rate), and high-density recordings from Purkinje cells across different layers in awake animals, significantly limits the throughput of data collection. Second, the statistical outcomes obtained from our analyses, which combine multiple techniques, are robust and provide a strong basis for our conclusions. Third, the current study already involves a substantial number of animals (74 mice), which aligns with ethical considerations for minimizing animal use while ensuring robust results.

We believe that the current sample size is sufficient to support the findings presented in the manuscript. Expanding the sample size further would require considerable additional resources and time, without a clear indication that it would fundamentally alter the conclusions of the study. We are grateful for the reviewer’s understanding of these limitations and their acknowledgment of the value of the current dataset.

(10) tDCS and tES seem to be used interchangeably; please make it consistent.

We agree that this could cause confusion. To address this, we have added a clarification at the first mention of tES in the manuscript, indicating that tES (transcranial Electrical Stimulation) is an umbrella term that encompasses both tDCS (transcranial Direct Current Stimulation) and tACS (transcranial Alternating Current Stimulation). We have ensured consistent use of the appropriate term throughout the rest of the text.

(11) Did the authors apply saline or agar to the craniotomy while recording? Or was the dura dried out? Can the authors clarify this, and relate the answer to a potential interaction of either the medium or dryness of the dura with the tDCS?

We appreciate the reviewer’s inquiry. To prevent the dura from drying out during our recordings, we applied saline to the cranial window throughout the experiment. Additionally, in our setup, the tDCS ring-shaped electrode was placed over the skull and sealed with dental cement to prevent any leakage of currents into the craniotomy, which was positioned at the center of the preparation. This precaution also helped minimize electrical noise reaching the recording electrode. In instances where the seal was not perfectly executed, the electrical noise from tDCS leaked into the saline solution, causing amplifier saturation and rendering neuronal activity recordings impossible.

(12) There are several mistakes in spelling and grammar throughout the document; please check carefully.

We appreciate the reviewer’s attention to detail regarding spelling and grammar. We have carefully reviewed the manuscript and corrected all identified errors to ensure clarity and proper language use throughout the document.

(13) Can the authors briefly explain why tACS (and not tDCS) is used to measure the effectiveness of the stimulation at the different depths as shown in Figure 1? As the rest of the paper focuses entirely on tDCS, it is important to understand why tACS is used in Figure 1.

We will clarify this distinction. We chose tACS for measuring electric field strength for two main reasons:

• Amplifier Limitations: The amplifiers commonly used in electrophysiology are designed to filter out low-frequency components, including direct current (DC) signals, using a highpass filter. This is due to the fact that the neuronal signals of interest, such as action potentials, typically occur at higher frequencies (several Hz to kHz). Consequently, any DC signal applied is filtered out from the recordings, preventing us from measuring changes in voltage effectively.

• Impedance Changes: DC stimulation can alter the impedance of electrodes and surrounding tissue over time. To mitigate this effect and maintain stable recordings, it is advantageous to frequently alternate the polarity and intensity of the stimulation.

This next text has been included in the 'Transcranial Electrical Stimulation' section of the 'Materials and Methods' part of the manuscript:

“We selected tACS to measure electric field strength due to two main reasons: (1) amplifiers used in electrophysiology filter out low-frequency signals like DC, making voltage changes from tDCS undetectable, and (2) DC stimulation can alter electrode and tissue impedance over time, whereas alternating the polarity in tACS helps maintain stable recordings.”

It is important to note that our aim with tACS is to provide an approximation of current propagation through the tissue, rather than to exactly replicate the baseline conditions encountered during continuous tDCS stimulation.

(14) How do Figures 2e and f relate to each other? Figure 2e has 6 red lines, but 6f has 8 red explicitly states that 8 cells were recorded.

We appreciate the Reviewer for highlighting this discrepancy. You are correct that in Figure 5e, the lines are too densely packed to easily distinguish all of them. Additionally, the activity of two neurons under anodal tDCS was greatly suppressed, which caused their corresponding arrowheads to be close to the origin of the arrows, making them less visible. To clarify, while Figure 5f shows all 8 cells recorded, the compression of the data in Figure 5e makes it challenging to distinguish all individual responses visually. We have added a clarifying note to the figure legend to explaining that “densely packed lines and suppressed activity of two neurons under anodal tDCS reduce the visibility of their responses”.

(15) Figure 2g contains two outliers that seem critical to the correlation, this is noticeable as nearly all other cells seem to modulate much more modestly. Maybe add a few more cells to convince everyone?

We agree with the reviewer that the two neurons in Figure 2g could appear as outliers. To address this, we applied the ROUT method with a stringent Q = 1% to detect potential outliers, and none were found. In addition, we have confirmed the robustness of our results by performing a complementary analysis using robust linear regression methods (e.g., M-estimators), which showed consistent findings with our original analysis. For this purpose, we used the 'Huber' loss function, which combines least squares with robustness against outliers. The regression line obtained with this method (y = -0.5650x + 157.4556) differs minimally from the originally presented value, with the p-value of the slope and the intercept being p = 1.4846x10^-4 (t₍₂₂₎ = -4.5740) and p = 1.1382x10^-11 (t₍₂₂₎ \= 12.8010), respectively. Author response image 1 both regression fits to facilitate their comparison. These additional steps ensure the reliability of the relationship observed in the figure, even when accounting for the potential influence of the two data points.

(16) 'From these experiments we can conclude that 1) tDCS in vermis of anesthetized mice modulates PCs and non-PCs in a heterogeneous way'. Figure 4d shows no correlation between cathodal versus anodal stimulation for non-PCs, so how does the data suggest heterogeneous modulation of non-PCs? Is it simply heterogeneous because the data is very scattered?

Thank you for your observation. By 'heterogeneous modulation,' we indeed refer to the scattered nature of the responses in non-PCs. Although Figure 4d shows a wide spread of data points and the linear regression is not statistically significant, a general trend can still be observed, where 11 out of 15 non-PCs show modulation in opposite directions with anodal and cathodal tDCS. However, this trend is not consistent across all neurons, hence our description of this modulation as heterogeneous. Importantly, this contrasts with the response observed in Purkinje cells (PCs), where a more consistent modulation pattern is evident, and the p-value for the linear regression is significant. Therefore, we conclude that while PCs show a clearer, more predictable modulation, the scattered data in non-PCs supports a more heterogeneous response.

(17) The authors state that it is not possible to discriminate the non-PCs, even though some published papers suggest this is quite possible (see e.g., work by Simpson and Ruigrok; please discuss). For sure, the authors of the current manuscript should be able to discriminate the interneurons in the molecular layer from those in the granular layer (if it were only by identifying the polarity of the complex spikes). The authors may want to consider redoing the analyses of the non-PCs, and at least present and compare the outcomes of these two main subgroups of non-PCs.

The authors are indeed familiar with the work of Simpson, Ruigrok, and others in linking electrophysiological recordings with neuronal class identity. Prior to proceeding with juxtacellular labeling, we conducted preliminary attempts to categorize non-PC neurons based on firing characteristics. However, we ultimately chose not to include neuronal sorting for non-PCs in this study for two main reasons. 

First, the baseline recording period without tDCS was very short (10 seconds), and once tDCS was applied, the firing rate, coefficient of variation, and interspike intervals (ISI) of neurons were already altered. This made it difficult to reliably classify neurons based on their spontaneous activity, which is critical for precise sorting.

Second, unlike PCs—where the presence of complex spikes and the resulting inhibition provide a clear ground truth—there is no analogous, unequivocal marker for non-PCs. Even following the reviewer's suggestion, while it might be possible in the molecular layer to identify a neuron as a molecular layer interneuron (MLI), this approach does not allow for a rigorous distinction between basket cells and stellate cells. These two cell types, despite their distinct morphologies—which could significantly affect their responses to tDCS—cannot be reliably differentiated without a true ground truth. Therefore, in the absence of such definitive markers, we believe that further subclassification of non-PCs based solely on electrophysiological properties would not be sufficiently rigorous for the purposes of our study.

(18) Can the authors briefly discuss possible reasons why non-PCs in Crus1/2 do show heterogeneous responses similar to that of PCs, whereas the non-PCs in the vermis do not?

We appreciate the reviewer’s insightful question regarding the different modulation patterns observed in non-PCs between Crus I/II and the vermis. Several potential factors could contribute to these differences, including variations in local cerebellar circuit connectivity between the two regions, differences in the cellular diversity of non-PCs due to the lack of a "ground truth" for their classification, or disparities in somatodendritic orientation and cell distribution. In the vermis, PCs are organized into different layers with opposing orientations (as shown in Figure 6), which could result in a more stable, polarity-dependent modulation, making their response more distinct from that of non-PCs. In contrast, in Crus I/II, the orientation of PCs is more heterogeneous and less aligned with the electric field, potentially leading to a more variable modulation pattern in both PCs and non-PCs. 

However, it is important to note that we did not aim to juxtacellularly label non-PCs in this study, so we cannot offer a definitive answer regarding their precise orientation or identity. Additionally, the observed differences could be partially attributed to statistical power: we recorded 50 nonPCs in Crus I/II compared to only 25 in the vermis. Out of the 15 neurons in the vermis that showed statistically significant modulation, 11 displayed polarity-dependent modulation in opposite directions, but the smaller sample size might have limited our ability to detect the full range of possible effects. Furthermore, recordings in Crus I/II were conducted in awake animals, whereas the neurons recorded in Figure 4 in the vermis were obtained from anesthetized animals. This difference in physiological state could also be related to the observed changes.

(19) 'The importance of PC axodendritic orientation in determining the effect of tDCS on firing rate modulation is further highlighted by our observation that pre-synaptic non-PC neurons providing inputs to PCs modulate their activity in a very heterogeneous way.' This is based on the finding that non-PCs modulate heterogeneously, but that is not what is shown for the vermis. Please address.

Thank you for pointing this out. By 'heterogeneous modulation,' we are referring to the observation that non-Purkinje cells (non-PCs) respond in various ways under tDCS. Specifically, some nonPCs increase their activity under anodal stimulation and decrease it under cathodal stimulation (and vice versa), while others exhibit more complex patterns, such as increasing their activity under both anodal and cathodal stimulation or decreasing for both polarities. Additionally, some non-PCs only respond to one polarity, and others show no response at all.

Our reasoning is that if the presynaptic non-PCs providing inputs to Purkinje cells (PCs) were the primary drivers of PC modulation, we would expect them to behave in a manner opposite to how PCs are modulated. For instance, if most non-PCs increased their activity under anodal stimulation while PCs decreased theirs, this could suggest that tDCS modulates non-PCs to fire more, imposing greater inhibition on PCs since many non-PCs are inhibitory. However, what we observe is a highly heterogeneous response from non-PCs, with no clear pattern that would consistently explain the modulation of PCs through presynaptic inputs alone. While non-PCs must certainly exert some influence on PC activity, their variable responses suggest that the modulation of PCs may also be driven by direct effects of tDCS on the PCs themselves, in addition to any indirect presynaptic influence.

(20) To help in reinforcing the hypothesis that stimulation response depends on dendritic orientation, the authors could show, with the existing data, how PCs in different layers of the vermis respond to cathodal or anodal stimulations. The data shown in Figure 4a-c already has a large number of PCs recorded in different layers of the vermis. As shown in Figure 4b, PCs in specific layers of the vermis have specific dendritic orientations. Can the authors show that PCs recorded for Figure 4, in the different layers (implying similar dendritic orientation) have similar (or different) stimulation responses? This would greatly improve their argument for the importance of dendritic orientation for tDCS responses.

We appreciate the reviewer’s suggestion and the valuable insight it provides. In fact, this was one of the main motivations for performing the experiments shown in Figure 6, where we conducted simultaneous recordings of different Purkinje cells (PCs) in distinct layers. This allowed us to directly compare responses in neurons with different somatodendritic orientations. Unfortunately, the data presented in Figure 4 were obtained using glass micropipettes for juxtacellular labeling— a method that permits recording from only one neuron at a time—thus precluding a robust analysis of the correlation between dendritic orientation and tDCS responses. Furthermore, it should be noted that Figure 4a represents an idealized approximation; since these recordings were performed in different animals with variations along the anteroposterior axis, precise dendritic orientation cannot be reliably attributed to each cell (except for those that were juxtacellularly labeled).

Additionally, unlike recordings with Neuropixels, where we have numerous contacts positioned at known distances from each other, enabling us to precisely locate cells within the cerebellar layers, the localization of neurons recorded with glass pipettes is less accurate. This is due to factors such as tissue displacement during insertion and animal movements, which further complicates the precise determination of neuronal layer placement during the stimulation protocol.

While the data in Figure 4 do not allow us to definitively test our hypothesis, the results shown in Figure 6 provide a more direct comparison of the responses of PCs across different layers to tDCS, thereby reinforcing the hypothesis that dendritic orientation is a key factor in modulating neuronal activity.

(21) The data shown in Figure 5e-f feels underpowered, although the statistical correlation between dendritic orientation and response is strong. For example, currently, the authors show that at an angle of ~0 degrees, two cells increase their firing to anodal stimulation, and 1 cell at 180 ~degrees decreases its firing. Again, the manuscript would be much improved if the authors could increase the sample sizes for these experiments.

We appreciate the reviewer’s concern regarding the sample size in Figure 5e-f. While the statistical correlation between dendritic orientation and response to tDCS is strong, we understand that the data may feel underpowered, particularly given the limited number of cells observed at specific angles such as ~0 degrees and ~180 degrees.

It’s important to note that although visually it may appear there is only one neuron at 180 degrees during anodal stimulation, there are actually three neurons at this orientation. This is more clearly visible in the same figure during cathodal stimulation. However, the firing rate of these neurons during anodal stimulation is so low that the arrow representing their response appears very small, making it difficult to distinguish. (We have added a clarifying note to the figure legend to explaining that “densely packed lines and suppressed activity of two neurons under anodal tDCS reduce the visibility of their responses”).

Unfortunately, increasing the sample size for these specific experiments is not feasible within the current study due to the technical complexity and time-consuming nature of the recordings, especially when incorporating juxtacellular labeling or high-density electrode arrays. Despite these challenges, we believe the current sample provides valuable insights into the relationship between dendritic orientation and firing rate modulation under tDCS. The significant statistical correlation suggests that the observed trend is robust, even with the existing sample size. Additionally, the different experimental approaches used in this study—single-unit extracellular recordings in different regions of the cerebellum in both awake and anesthetized animals, juxtacellular recordings and labeling, and high-density multi-unit recordings—provide a robust and comprehensive view of the results. Each technique offers complementary insights, strengthening our conclusions and ensuring that the observed patterns are not the result of one specific method or condition. Future studies could aim to expand on these findings, but we are confident that the results presented here contribute meaningfully to our understanding of how dendritic orientation influences neuronal responses to tDCS.

(22) The authors, rightly so, address the potential impact of plasticity in the discussion. Here, the authors may want to cite other studies that have directly addressed this question: E.g., Das et al., 2017 (Frontiers Neuroscience, 11:444; doi: 10.3389/fnins.2017.00444) and van der Vliet et al., 2018 (Brain Stimul, 11(4):759-771; doi: 10.1016/j.brs.2018.04.009).

We appreciate the reviewer’s suggestion to include additional studies addressing the impact of plasticity on the effects of cerebellar tDCS. In response, we have added a new sentence in the discussion section that cites both Das et al. (2017) and van der Vliet et al. (2018), highlighting the importance of synaptic plasticity in the effects of tDCS. 

“These findings are consistent with previous work suggesting that synaptic plasticity is crucial for the effects of tDCS, as demonstrated by the importance of PC plasticity in behavioral outcomes(51) and the role of BDNF-mediated plasticity in motor learning(52).”

Reviewer #2 (Recommendations for the authors):

In the introduction, it would be beneficial to provide additional context regarding the influence of neuronal orientation on modulation shown from in-vitro studies. In addition, some explanation of the uniformity/non-uniformity of the electrical field would help. From here, the authors should provide their specific hypotheses for these experiments.

We thank the Reviewer #2 for this insightful comment. In response, we have expanded the introduction to provide a clearer context regarding the influence of neuronal orientation on the effects of tDCS. Therefore, we have added two new paragraphs in the Introduction to address these points.

“For neurons whose somatodendritic axis is aligned with the electric field, the field induces a pronounced somatic polarization. In the case of anodal stimulation, where the positive electrode is positioned near the dendrites and the soma is oriented away, positively charged ions accumulate near the soma, leading to depolarization and increased excitability, thus facilitating action potential generation. Conversely, neurons whose orientation opposes the field, such as when the soma is closer to the positive electrode and the dendrites face away, experience hyperpolarization, reducing excitability. Lastly, neurons oriented perpendicular to the electric field would exhibit minimal somatic polarization, as the field does not induce significant redistribution of charges along the somatodendritic axis.”

Additionally, we have now clarified our a priori hypothesis regarding neuronal orientation and its expected influence on tDCS efficacy.

“We hypothesized that the orientation of PCs relative to the electric field would influence the effects of tDCS on neural activity. In the Vermis, PCs oriented parallel to the field are expected to exhibit stronger effects due to greater somatic polarization, leading to depolarization or hyperpolarization depending on the orientation of the somatodendritic axis. Conversely, PCs in Crus I/II, which are oriented obliquely to the field, are expected to exhibit intermediate effects, as the oblique alignment reduces the strength of polarization compared to parallel alignment.”

Justification of the stimulation parameters used (i.e., intensity and pattern) should be included in the Methods.

The time of stimulation was chosen of only a few seconds to avoid confounding effects of plasticity, which is known to require several minutes of tDCS administration. Regarding the intensities, we refer to previous studies from our lab, using the exact same methodology, where we find that 100, 200 and 300 µA were ideal to obtain reliable and robust results in neuronal modulation, while keeping animal awareness of the stimulation at a minimum level. We also added the clarification to the main text.

Please also justify the use of tACS rather than tDCS in the first experiment.

We appreciate Reviewer #2’s assessment of the differences between tDCS and tACS. We will clarify this distinction. We chose tACS for measuring electric field strength for two main reasons:

• Amplifier Limitations: The amplifiers commonly used in electrophysiology are designed to filter out low-frequency components, including direct current (DC) signals, using a highpass filter. This is due to the fact that the neuronal signals of interest, such as action potentials, typically occur at higher frequencies (several Hz to kHz). Consequently, any DC signal applied is filtered out from the recordings, preventing us from measuring changes in voltage effectively.

• Impedance Changes: DC stimulation can alter the impedance of electrodes and surrounding tissue over time. To mitigate this effect and maintain stable recordings, it is advantageous to frequently alternate the polarity and intensity of the stimulation.

This next text has been included in the 'Transcranial Electrical Stimulation' section of the 'Materials and Methods' part of the manuscript:

“We selected tACS to measure electric field strength due to two main reasons: (1) amplifiers used in electrophysiology filter out low-frequency signals like DC, making voltage changes from tDCS undetectable, and (2) DC stimulation can alter electrode and tissue impedance over time, whereas alternating the polarity in tACS helps maintain stable recordings.”

It is important to note that our aim with tACS is to provide an approximation of current propagation through the tissue, rather than to exactly replicate the baseline conditions encountered during continuous tDCS stimulation.

Reviewer #3 (Recommendations for the authors):

(1) A suggestion would be to highlight which of the data points in Figure 2g are the neurons they show as representative in Figure 2e-f. This would give the reader insights into how a standard neuron would behave/how representative these neurons are.

We appreciate the reviewer’s comment and, in response, we have highlighted the two exemplary neurons from Figures 2e-f in Figure 2g to provide better insight into how these representative neurons behave in the context of the overall data. This will help the reader understand how typical these neurons are in relation to the broader dataset. Additionally, we have applied the same approach to Figure 3, highlighting the representative neurons for further clarity.

(2) It would also be interesting to add figures to the supplementary materials that show the waveforms of non-PC neurons during anodal and cathodal tDCS, as done for PC neurons in the supplementary materials (as stated at the bottom of page 14, the authors chose to mention but not show these).

We understand the reviewer’s interest in visualizing the waveforms of non-Purkinje neurons during anodal and cathodal tDCS. To address this, we have carefully examined the waveforms of both non-Purkinje neurons under these conditions. However, given the absence of notable changes in their waveforms, we believe that this data does not have sufficient standalone significance to justify the inclusion of a new figure. We are, of course, happy to provide this data upon request or to incorporate it into the supplementary materials if deemed necessary.

Author response image 7.

Superimposed averaged SS waveforms under control (black), anodal (red) and cathodal (blue) tDCS from the example neurons shown in panels A and B in Fig. 3.

(3) In Figure 5d, there is a significant aftereffect of the stimulation on the Purkinje cell firing rate - do the authors have an idea why this occurred?

We appreciate the reviewer’s observation, as it highlights an interesting phenomenon that we have not been able to fully explain. We observed this aftereffect in many of the recorded neurons, and intriguingly, it often occurred in the opposite direction to the modulation seen during tDCS. We addressed a potential explanation for this in the discussion section:

‘Nonetheless, we cannot rule out the possibility of indirect synaptic effects. Indeed, the electric field gradient imposed by tDCS could indirectly modulate a specific neuron firing rate by increasing (or decreasing) its pre-synaptic activity, i.e. by modulating the firing rate of other neurons that synapse onto it. Indeed, these synaptic changes could explain the rebound effect observed after tDCS termination. The synapses involved in the modulation of firing rate may undergo a short-term plasticity process(47–50), which can continue to affect the firing rate even after the external currents have been turned off and no polarization is exerted on the neuron. These findings are consistent with previous work suggesting that synaptic plasticity is crucial for the effects of tDCS, as demonstrated by the importance of PC plasticity in behavioral outcomes(51) and the role of BDNF-mediated plasticity in motor learning(52).’

This explanation highlights the potential role of synaptic plasticity and the indirect modulation of neuronal networks, but further investigation would be required to fully understand the mechanisms underlying this aftereffect.

(4) I'm having trouble understanding the reference electrode positioning from schematics 1a & 1b: The text and 1a suggest that the reference electrode was positioned on the back of the mouse, outside of the brain. But Figure 1b looks as if the reference electrode was on the mouse cerebral cortex. Could the authors adapt schematic 1b to clarify the reference location or add this information to the legend?

We agree that the figure showing two different reference electrodes was confusing, and we have now modified it to better clarify the distinction between the recording reference electrode and the stimulation reference electrode. Additionally, we have specified in Figures 1A and 1B whether the reference pertains to the transcranial alternating stimulation or to the electrophysiological recording.

(9) In the discussion, (page 22) the authors highlight the importance of axodendritic orientation, but they analyze only somatodendritic orientation. Are the two so similar that they can be used synonymously? This would be good to clarify.

We appreciate the reviewer’s clarification and fully agree. While Purkinje cells (PCs) do indeed have a highly polarized morphology, with the axon generally oriented in the opposite direction to the main dendrites, this is not always the case, especially for other types of neurons. Therefore, our results strictly refer to the somatodendritic axis, as this is the one we can most clearly observe through our juxtacellular labeling. In response, we have changed all instances where the term 'axodendritic' appeared in the text to 'somatodendritic' for accuracy.

(10) It would be helpful to clarify that Supplementary Figure 3b and 3e are the same as Figures 4 c and 4d, respectively. This was confusing to me.

We appreciate the reviewer’s feedback and have now modified the caption of Supplementary Figure 3 to indicate that Supplementary Figures 3b and 3e correspond to Figures 4c and 4d, respectively. This should help clarify any confusion.

(11) Typo: 'consisting in' ◊ consisting of

We thank the reviewer for their clarification. The typo has been corrected to 'consisting of'.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In the study "Re-focusing visual working memory during expected and unexpected memory tests" by Sisi Wang and Freek van Ede, the authors investigate the dynamics of attentional re-orienting within visual working memory (VWM). Utilizing a robust combination of behavioral measures, electroencephalography (EEG), and eye tracking, the research presents a compelling exploration of how attention is redirected within VWM under varying conditions. The research question addresses a significant gap in our understanding of cognitive processes, particularly how expected and unexpected memory tests influence the focus and re-focus of attention. The experimental design is meticulously crafted, enabling a thorough investigation of these dynamics. The figures presented are clear and effectively illustrate the findings, while the writing is concise and accessible, making the complex concepts understandable. Overall, this study provides valuable insights into the mechanisms of visual working memory and attentional re-orienting, contributing meaningfully to the field of cognitive neuroscience. Despite the strengths of the manuscript, there are several areas where improvements could be made.

We thank the reviewer for this summary and positive appraisal of our study and our findings. In addition, we are of course grateful for the excellent suggestions for improvements that we have embraced to further strengthen our article. 

Microsaccades or Saccades?

In the manuscript, the terms "microsaccades" and "saccades" are used interchangeably. For instance, "microsaccades" are mentioned in the keywords, whereas "saccades" appear in the results section. It is crucial to differentiate between these two concepts. Saccades are large, often deliberate eye movements used for scanning and shifting attention, while microsaccades are small, involuntary movements that maintain visual perception during fixation. The authors note the connection between microsaccades and attention, but it is not well-recognized that saccades are directly linked to attention. Despite the paradigm involving a fixation point, it remains unclear whether large eye movements (saccades) were removed from the analysis. The authors mention the relationship between microsaccades and attention but do not clarify whether large eye movements (saccades) were excluded from the analysis. If large eye movements were removed during data processing, this should be documented in the manuscript, including clear definitions of "microsaccades" and "saccades." If such trials were not removed, the contribution of large eye movements to the results should be shown, and an explanation provided as to why they should be considered.

We thank the reviewer for raising this relevant point. Before turning to this relevant distinction, we first wish to clarify how, for our main aim of tracking the dynamics of ‘re-orienting in working memory’, any spatial modulation in gaze – be it driven by micro- or macro-saccades – suits this purpose. Having made this explicit, we also fully agree that disambiguating the nature of the saccade bias during internal focusing has additional value.

Because it is notoriously challenging (or at least inherently arbitrary) to draw an absolute fixed boundary between macro- and microsaccades, we instead decided to adopt a two-stage approach to our analysis (building on prior studies from our lab, e.g., de Vries et al., 2023; Liu et al., 2023; Liu et al., 2022). In the first step, we analysed spatial biases in all detected saccades no matter their size (hence our labelling of them as “saccades” when describing these analyses). In a second step, we decomposed and visualized the saccade-rate effect as a function of saccade size in degrees. This second stage directly exposed the ‘nature’ of the saccade bias, as we visualized in Figure 2c (with time on the x axis, saccade size on the y axis, and the spatial modulation color coded). Because these visualizations directly address this major comment, we have now made these key set of results much clearer in our work (we agree that our original visualization of this key aspect of our data was suboptimal). In addition, we have added similar plot for the saccade data in the test-phase in Supplementary Figure S2b.

These complementary analyses show how the saccade bias (more toward than away saccades) is indeed predominantly driven by small saccades (hence are labelling as “micro-saccades” when interpreting our findings), and less so by larger saccades associated with looking back all the way to the location where the memory item had been presented at encoding (positioned at 6 degrees). This is important as it helps to arbitrate between fixational/micro-saccadic eye-movement biases (previously associated with covert and internal attention shifts; cf. de Vries et al., 2023; Engbert and Kliegl, 2003; Hafed and Clark, 2002; Liu et al., 2023; Liu et al., 2022) vs. larger eye movements back to the original locations of the item (previously associated with ‘looking at nothing’ during memory retrieval and imagery; cf. Brandt and Stark, 1997; Ferreira et al., 2008; Johansson and Johansson, 2014; Laeng et al., 2014; Martarelli and Mast, 2013; Spivey and Geng, 2001). By adopting this visualization, we can show this while preserving the richness of our data, and without having to a-priori set an (inherently arbitrary) threshold for classifying saccades as either “macro” or “micro”.

Having explained our rationale, we nevertheless agree with the reviewer that it is worth showing how our time course results hold up when only considering fixational eye movements below 2 visual degrees, which we consider “fixational” provided that our memory stimuli at encoding were presented at 6 visual degrees from central fixation. We show this in Supplementary Figure S1. As can be seen below, our main saccade bias results stay almost the same when restricting our analyses exclusively to fixational saccades within 2 degrees, both when considering our data after the retrocue (Supplementary Figure S1a) as well as after the memory test (Supplementary Figure S1b).

Because we agree this is important complementary data, we have now added this as supplementary figures. In addition, we have added the results to our article. We also point to these additional corroborating findings at key instances in our article:  

Page 5 (Results)

“As in prior studies from our lab with similar experimental set-ups, internal attentional focusing was predominantly driven by fixational micro-saccades (small, involuntary eye-movements around current fixation). To reveal this in the current study, we decomposed and visualized the observed saccade-rate effect as a function of saccade size (Figure 2c), following the same procedure as we have adopted in other recent studies on this bias (de Vries et al., 2023; Liu et al., 2023; Liu et al., 2022). As shown in the saccade-size-over-time plots in Figure 2c, also in the current study, the difference between toward and away saccades (with red colours denoting more toward saccades) was predominantly driven by fixational saccades in the micro-saccades range (< 2°).”

“Moreover, as shown in Supplementary Figure S1a, complementary analyses show that our time course (saccade bias) results hold even when exclusively considering eye movements below 2 visual degrees that we defined as “fixational” provided that the memory items were presented 6 visual degrees from the fixation during encoding. This further corroborates that the bias observed during internal attentional focusing was predominantly driven by fixational micro-saccades rather than looking back to the encoded location of the memory items (cf. Johansson and Johansson, 2014; Richardson and Spivey, 2000; Spivey and Geng, 2001; Wynn et al., 2019).”

Page 7 (Results):

“As shown in the corresponding saccade-size-over-time plots in Supplementary Figure S2b, consistent with what we observed following the cue, the difference between toward and away saccades following the test was again predominantly driven by saccades in the fixational microsaccade range (< 2°), and the time course (saccade bias) results hold even when exclusively considering fixational eye movements below 2 visual degrees (Supplementary Figure S1b). Thus, just like mnemonic focusing after the cue, re-orienting after the memory test was also predominantly reflected in fixational micro-saccades, and not looking back at the original location of the memory items that were encoded at 6 degrees away from central fixation.”

Alpha Lateralization in Attentional Re-orienting

In the attentional orienting section of the results (Figure 2), the authors effectively present EEG alpha lateralization results with time-frequency plots and topographic maps. However, in the attentional reorienting section (Figure 3), these visualizations are absent. It is important to note that the time period in attentional orienting differs from attentional re-orienting, and consequently, the time-frequency plots and topographic maps may also differ. Therefore, it may be invalid to compute alpha lateralization without a clear alpha activity difference. The authors should consider including timefrequency plots and topographic maps for the attentional re-orienting period to validate their findings.

We thank the reviewer also for this constructive suggestion. The reason we did not expand on the time-frequency maps and topographies at the test-stage was the relative lack of alpha effects at the test stage (compared to the clearer alpha modulations after the retrocue). Nevertheless, we agree that including these data will increase transparency and the comprehensiveness of our article. We now added time-frequency plots and topographic maps for alpha lateralization in response to the workingmemory test in Supplementary Figure S2. As can be seen, the time-frequency plots and topographies in the re-focusing period after the working-memory test were consistent with our time-series plots in Figure 3a – reinforcing how alpha lateralization is generally not clear following the working-memory test. In accordance with this relevant addition, we added the following in the revised manuscript:

Page 7 (Results):

“For complementary time-frequency and topographical visualizations, see Supplementary Figure S2a.”

Onset and Offset Latency of Saccade Bias

The use of the 50% peak to determine the onset and offset latency of the saccade bias is problematic. For example, if one condition has a higher peak amplitude than another, the standard for saccade bias onset would be higher, making the observed differences between the onset/offset latencies potentially driven by amplitude rather than the latencies themselves. The authors should consider a more robust method for determining saccade bias onset and offset that accounts for these amplitude differences.

We thank the reviewer for raising this valuable point. We agree that the calculation of onset and offset latencies of the saccade bias could be influenced by the peak amplitude of the waveforms. Thus, we further conducted the Fractional Area Latency (FAL) analysis on the comparison of the saccade bias following the working-memory test between valid cue (expected test) and invalid cue (unexpected test) trials. The FAL analysis has been commonly applied to Event-Related Potentials (ERPs) to estimate the latency of ERP components (Hansen and Hillyard, 1980; Luck, 2005). Instead of relying on the peak latency, the FAL method calculates latency based on a predefined fraction of the area under the waveform. This can provide a more robust measure of component latency. Prompted by this comment, we now also applied FAL analysis to our saccade bias waveforms. This corroborated our original conclusion. Because we believe this is an important complement, we now added these additional outcomes to our article: 

Page 9 (Results): 

“We additionally conducted Fractional Area Latency (FAL) analysis on the comparison of the saccade bias following the memory test between valid- and invalid-cue trials to rule out the potential contribution of peak amplitude differences into the onset and offset latency differences (Hansen and Hillyard, 1980; Kiesel et al., 2008; Luck, 2005). Consistent with our jackknife-based latency analysis, the FAL analysis revealed a significantly prolonged saccade bias following the unexpected tests (the invalid-cue trials) vs. expected tests (the valid-cue trials) in both 80% and 60% cue-reliability conditions (411 ms vs. 463 ms, t₍₁₄₎ = 2.358, p = 0.034; 417 ms vs. 468 ms, t₍₁₅₎ = 2.168, p = 0.047; for 80% and 60%, respectively). Again, there was no significant difference in onset latency following unexpected vs. expected tests. (346 ms vs. 374 ms, t₍₁₄₎ = 2.052, p = 0.060; 353 ms vs. 401 ms, t₍₁₅₎ = 1.577, p = 0.136; for 80% and 60%, respectively).”

In accordance, we also added the following to our Methods:

Page 18 (Methods): 

“In addition to the jackknife-based latency analysis, we further applied a Fractional Area Latency (FAL) method to the saccade bias comparison between validly and invalidly cued memory tests to rule out the contribution of the peak amplitude difference into the onset and offset latency difference (Hansen and Hillyard, 1980; Kiesel et al., 2008; Luck, 2005). We first defined the onset and offset latency of the saccade bias as the first time point at which 25% or 75% of the total area of the component has been reached, relative to a lower boundary of a difference of 0.3 Hz between toward and away saccades (to remove the influence of noise fluctuations in our difference time course below this lower boundary). The extracted onset and offset latency for all participants was then compared using paired-samples t-tests.”

Control Analysis for Trials Not Using the Initial Cue

The control analysis for trials where participants did not use the initial cue raises several questions:

(1) The authors claim that "unlike continuous alpha activity, saccades are events that can be classified on a single-trial level." However, alpha activity can also be analyzed at the single-trial level, as demonstrated by studies like "Alpha Oscillations in the Human Brain Implement Distractor Suppression Independent of Target Selection" by Wöstmann et al. (2019). If single-trial alpha activity can be used, it should be included in additional control analyses.

We agree with the reviewer that alpha activity can also be analyzed at the single-trial level. However, because alpha is a continuous signal, single-trial alpha activity will necessarily be graded (trials with more or less alpha power). This is still different from saccades, that are not continuous signals but true ‘events’ (either a saccade was made, or no saccade was made, with no continuum in between). Because of this unique property, it is possible to sort trials by whether a saccade was present (and, if present, by its direction), in an all-or-none way that is not possible for alpha activity that can only be sorted by its graded amplitude/power. This is the key distinction underlying our motivation to sort the trials based on saccades, as we now make clearer: 

Page 10 (Results): 

“Although alpha can also be analyzed as the single trial level (e.g. Macdonald et al., 2011; Wöstmann et al., 2019; for a review, see Kosciessa et al., 2020), saccades offer the unique opportunity to split trials not by graded amplitude fluctuations but by discrete all-or-none events.” 

In addition, please note how our saccade markers were also more reliable/sensitive, especially in the subsequent memory-test-phase of interest. This is another reason we decided to focus this control analysis on saccades and not alpha activity. 

(2) The authors aimed to test whether the re-orienting signal observed after the test is not driven exclusively by trials where participants did not use the initial cue. They hypothesized that "in such a scenario, we should only observe attention deployment after the test stimulus in trials in which participants did not use the preceding retro cue." However, if the saccade bias is the index for attentional deployment, the authors should conduct a statistical test for significant saccade bias rather than only comparing toward-saccade after-cue trials with no-toward-saccade after-cue trials. The null results between the two conditions do not immediately suggest that there is attention deployment in both conditions.

We thank the reviewer for bringing up this important point. We fully agree and, in fact, we had conducted the relevant statistical analysis for each of the conditions separately (in addition to their comparison). Upon reflection, we came to realize that in our original submission it was easy to overlook this point, and therefore thank the reviewer for flagging this. To make this clearer, we now also added the relevant statistical clusters in Figure 4a,b and more clearly report them in the associated text: 

Page 10 (Results):

“As we show in Figure 4a,b, we found clear gaze signatures of attentional deployment in response to expected (valid) memory tests, no matter whether we had pre-selected trials in which we had also seen such deployment after the cue in gaze (cluster P: 0.115, 0.041, 0.027, <0.001 for 80%-valid, 60%-valid, 80%-invalid, 60%-invalid trials, respectively), or not (cluster P: 0.016, 0.009, 0.001, <0.001 for 80%-valid, 60%-valid, 80%-invalid, 60%-invalid trials, respectively).”

(3) Even if attention deployment occurs in both conditions, the prolonged re-orienting effect could also be caused by trials where participants did not use the initial cue. Unexpected trials usually involve larger and longer brain activity. The authors should perform the same analysis on the time after the removal of trials without toward-saccade after the cue to address this potential confound.

We thank the reviewer for raising this. It is crucial to point out, however, that after any given 80% or 60% reliable cue, the participants cannot yet know whether the subsequent memory test in that trial will be expected (valid cue) or unexpected (invalid cue). Accordingly, the prolonged re-orienting after unexpected vs. expected memory tests cannot be explained by differential use of the cue (i.e., differential cue-use cannot be a “confound” for differential responses to expected and unexpected memory tests, as observed within the 80 and 60% cue-reliability conditions). 

Reviewer #2 (Public Review):

Summary:

This study utilized EEG-alpha activity and saccade bias to quantify the spatial allocation of attention during a working memory task. The findings indicate a second stage of internal attentional deployment following the appearance of a memory test, revealing distinct patterns between expected and unexpected test trials. The spatial bias observed during the expected test suggests a memory verification process, whereas the prolonged spatial bias during the unexpected test suggests a reorienting response to the memory test. This work offers novel insights into the dynamics of attentional deployment, particularly in terms of orienting and re-orienting following both the cue and memory test.

Strengths:

The inclusion of both EEG-alpha activity and saccade bias yields consistent results in quantifying the attentional orienting and re-orienting processes. The data clearly delineate the dynamics of spatial attentional shifts in working memory. The findings of a second stage of attentional re-orienting may enhance our understanding of how memorized information is retrieved.

Weaknesses:

Although analyses of neural signatures and saccade bias provided clear evidence regarding the dynamics of spatial attention, the link between these signatures and behavioral performance remains unclear. Given the novelty of this study in proposing a second stage of 'verification' of memory contents, it would be more informative to present evidence demonstrating how this verification process enhances memory performance.

We thank the reviewer for the positive summary of our work and for highlighting key strengths. We also appreciate the constructive suggestions, such as addressing the link between our observed refocusing signals and behavioral performance in our task. We now performed these additional analyses and added their outcomes to the revised article, as we detail in response to comment 2 below.  

Reviewer #2 (Recommendations For The Authors):

(1) Figure 2 shows graded spatial modulations in both EEG-alpha activity and saccade bias. However, while the imperative 100% cue conditions and 100% validity conditions largely overlap in EEG-alpha activity, a clear difference is present between these two conditions in saccade bias. The cause of the difference in saccade bias is unclear.

We thank the reviewer for pointing out this interesting difference. At this stage, it is hard to know with certainty whether this reflects a genuine difference in our 100% reliable and 100% imperative cue conditions that is selectively picked up by our gaze but not alpha marker. Alternatively, this may reflect differential sensitivity of our two markers to different sources of noise. Either way, we agree that this observation is worth calling out and reflecting on when discussing these results: 

Page 6 (Results):  

“It’s worth noting that while alpha lateralization shows very comparable amplitudes in the imperative-100% and 100% conditions, the saccade bias was larger following imperative-100% vs. 100% reliable cues. This may reflect a difference between these two cueing conditions that is selectively picked up by our gaze marker (though it may also reflect differential sensitivity of our two markers to different sources of noise). […]”

(2) Figure 3 shows signatures of attentional re-orienting after the memory test presented at the center. When the cue was not 100% valid, a noticeable saccade bias towards the memorized location of the test item was observed. This finding was explained as reflecting a re-orienting to the mnemonic contents. To strengthen this interpretation, I suggest providing evidence for the link between the attentional re-orienting signatures and memory performance.

We thank the reviewer for this constructive suggestion. We now sorted trials by behavioral performance using a median split on RT (fast-RT vs. slow-RT trials) and reproduction error (highaccuracy vs. low-accuracy trials).  Because we believe the outcomes of these analyses increase transparency as well as the comprehensiveness of our article, we have now included them as Supplementary Figure S3.

As shown below, we were able to link the saccade bias following the memory test to subsequent performance, but this reached significance only for the 80% valid-cue trials when splitting by RT (cluster P = 0.001). For the other conditions, we could not establish a reliable difference by our performance splits. Possibly this is due to a lack of sensitivity, given the relatively large number of conditions we had and, consequently, the relatively small number of trials we therefore had per condition (particularly in the invalid-cue condition with unexpected memory tests). We now bring forward these additional outcomes at the relevant section in our Results: 

Page 7 (Results):

“We also sorted patterns of gaze bias after the memory test by performance but could only establish a link between this gaze bias and RT following expected memory tests in our 80% cuereliability condition (cluster P = 0.001, Supplementary Figure S3). The lack of significant statistical differences in the remaining conditions may possibly reflect a lack of sensitivity (insufficient trial numbers) for this additional analysis.”

(3) When comparing the time course of attentional re-orienting after the memory test, a prolonged attentional re-orienting was observed for unexpected memory tests compared to the expected ones. While the onset latency was similar for unexpected and expected memory tests, the offset latency was prolonged for the unexpected memory test. Could this be attributed to the learned tendency to saccade toward the expected location in more valid trials? In this case, the prolonged re-orienting may indicate increased efforts in suppressing the previously learned tendency.

We thank the reviewer for bringing up this interesting possibility. In our original interpretation, this prolonged signal reflects a longer time needed to bring the unexpected memory content ‘back in focus’ before being able to report its orientation. At the same time, we agree that there are alternative explanations possible, such as the one raised by the reviewer. We now make this clearer when discussing this finding: 

Page 14 (Discussion): 

“[…] attentional deployment did become prolonged when re-focusing the unexpected memory item, likely reflecting prolonged effort to extract the relevant information from the memory item that was not expected to be tested. However, there may also be alternative accounts for this observation, such as suppressing a learned tendency to saccade in the direction of the expected item following an unexpected memory test.”

(4) To test whether the re-orienting signature is predominantly influenced by trials where participants delayed the use of cue information until the memory test appeared, the authors sorted the trials based on saccade bias after the initial cue. However, it would be more informative to depict the reorienting patterns by sorting trials based on memory performance. The rationale is that in trials where participants delayed using the initial retro-cue, memory performance (e.g., measured by reproduction error) might be less precise due to the extended memory retention period. Compared to saccade bias for initial orienting, memory performance could provide more reliable evidence as it represents a more independent measure.

We thank the reviewer for this suggestion. As delineated in response to comment 2, we now conducted this additional analysis and added the relevant outcomes to our article.  

(5) While the number of trials was well-balanced across blocks (~ 240 trials), how did the authors address the imbalance between valid and invalid trials, especially in the 80% cue validity block?

We thank the reviewer for raising this point.  First, we wish to point out that while trial numbers will indeed impact the sensitivity for finding an effect, trial numbers do not bias the mean – and therefore also not the comparison between means. In this light, it is vital to appreciate that our findings do not reflect a significant effect in valid trials but no significant effect in invalid trials (which we agree could be due to a difference in trial numbers), but rather a statistical difference between valid and invalid trials. This significant difference in the means between valid and invalid true cannot be attributed to a difference in trial numbers between these conditions. 

Having clarified this, we nevertheless agree that it is also worthwhile to empirically validate this assertion and show how our findings hold even when carefully matching the number of trials between valid and invalid conditions (i.e., between expected and unexpected memory tests). To do so, we ran a sub-sampling analysis where we sub-sampled the number of valid trials to match the number of invalid trials available per condition (and averaged the results across 1000 random sub-samplings to increase reliability). As anticipated, this replicated our findings of robust differences between the gaze bias following expected and unexpected memory tests in both our 80 and 60% cue-reliability conditions. We now present these additional outcomes in Supplementary Figure S4.

Because we agree this is an important re-assuring control analysis, we have now added this to our article:

Page 9 (Results):

“To rule out the possibility that the saccade-bias differences following expected and unexpected memory tests are caused by uneven trial numbers (200 vs. 50 trials in the 80% cuereliability condition, 150 vs. 100 trials in the 60% cue-reliability condition), we ran a subsampling analysis where we sub-sampled the number of valid trials to match the number of invalid trials available per condition (averaging the results across 1000 random sub-samplings to increase reliability). As shown in Supplementary Figure S4, this complementary subsampling analysis confirmed that our observed differences between the saccade bias following expected and unexpected memory tests in both 80% and 60% cue-reliability conditions are robust even when carefully matching the number of trials between validly cued (expected) and invalidly cued (unexpected) memory test.”

Reviewer #3 (Public Review):

Summary:

Wang and van Ede investigate whether and how attention re-orients within visual working memory following expected and unexpected centrally presented memory tests. Using a combination of spatial modulations in neural activity (EEG-alpha lateralization) and gaze bias quantified as time courses of microsaccade rate, the authors examined how retro cues with varying levels of reliability influence attentional deployment and subsequent memory performance. The conclusion is that attentional reorienting occurs within visual working memory, even when tested centrally, with distinct patterns following expected and unexpected tests. The findings provide new value for the field and are likely of broad interest and impact, by highlighting working memory as an action-bound process (in)dependent on (an ambiguous) past.

Strengths:

The study uniquely integrates behavioral data (accuracy and reaction time), EEG-alpha activity, and gaze tracking to provide a comprehensive analysis of attentional re-orienting within visual working memory. As typical for this research group, the validity of the findings follows from the task design that effectively manipulates the reliability of retro cues and isolates attentional processes related to memory tests. The use of well-established markers for spatial attention (i.e. alpha lateralization) and more recently entangled dependent variable (gaze bias) is commendable. Utilizing these dependent metrics, the concise report presents a thorough analysis of the scaling effects of cue reliability on attentional deployment, both at the behavioral and neural levels. The clear demonstration of prolonged attentional deployment following unexpected memory tests is particularly noteworthy, although there are no significant time clusters per definition as time isn't a factor in a statistical sense, the jackknife approach is convincing. Overall, the evidence is compelling allowing the conclusion of a second stage of internal attentional deployment following both expected and unexpected memory tests, highlighting the importance of memory verification and re-orienting processes.

Weaknesses:

I want to stress upfront that these weaknesses are not specific to the presented work and do not affect my recommendation of the paper in its present form.

The sample size is consistent with previous studies, a larger sample could enhance the generalizability and robustness of the findings. The authors acknowledge high noise levels in EEG-alpha activity, which may affect the reliability of this marker. This is a general issue in non-invasive electrophysiology that cannot be handled by the authors but an interested reader should be aware of it. Effectively, the sensitivity of the gaze analysis appears "better" in part due to the better SNR. The latter also sets the boundaries for single-tiral analyses as the authors correctly mention. In terms of generalizability, I am convinced that the main outcome will likely generalize to different samples and stimulus types. Yet, as typical for the field future research could explore different contexts and task demands to validate and extend the findings. The authors provide here how and why (including sharing of data and code).

We thank the reviewer for summarising our work and for carefully delineating its strengths. We also appreciate the mentioning of relevant generic limitations and agree that important avenues for future studies will be to expand this work with larger sample sizes, complementary measurement techniques, and complementary task contexts and stimuli.    

Reviewer #3 (Recommendations For The Authors):

In the conclusion, Wang and van Ede successfully demonstrate that attentional re-orienting occurs within visual working memory following both expected and unexpected tests. The conclusions are supported by the data and analyses applied, showing that attentional deployment is by the reliability of retro cues. Centrally presented memory tests can invoke either a verification or a revision of internal focus, the latter thus far not considered in both theory and experimental design in cognitive neuroscience.

I don't have any recommendations that will significantly change the conclusions.

We thank the reviewer for having carefully evaluated our work and hope the reviewer will also perceive the changes we made and the additional analyses we added in responses to the other two reviewers as further strengthening our article.

Reference

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Liu B, Alexopoulou SZ, van Ede F. 2023. Jointly looking to the past and the future in visual working memory. Elife.

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Li et al. investigates the metabolism-independent role of nuclear IDH1 in chromatin state reprogramming during erythropoiesis. The authors describe accumulation and redistribution of histone H3K79me3, and downregulation of SIRT1, as a cause for dyserythropoiesis observed due to IDH1 deficiency. The authors studied the consequences of IDH1 knockdown, and targeted knockout of nuclear IDH1, in normal human erythroid cells derived from hematopoietic stem and progenitor cells and HUDEP2 cells respectively. They further correlate some of the observations such as nuclear localization of IDH1 and aberrant localization of histone modifications in MDS and AML patient samples harboring IDH1 mutations. These observations are intriguing from a mechanistic perspective and they hold therapeutic significance, however there are major concerns that make the inferences presented in the manuscript less convincing.

(1) The authors show the presence of nuclear IDH1 both by cell fractionation and IF, and employ an efficient strategy to knock out nuclear IDH1 (knockout IDH1/ Sg-IDH1 and rescue with the NES tagged IDH1/ Sg-NES-IDH1 that does not enter the nucleus) in HUDEP2 cells. However, some important controls are missing.

A) In Figure 3C, for IDH1 staining, Sg-IDH1 knockout control is missing.

Thanks for the reviewer’s suggestion. We have complemented the staining of Sg-IDH1 knockout cells, and made corresponding revision in Figure 3C in the revised manuscript.

B) Wild-type IDH1 rescue control (ie., IDH1 without NES tag) is missing to gauge the maximum rescue that is possible with this system.

Thanks for the reviewer’s suggestion. We have overexpressed wild-type IDH1 in the IDH1-deficient HUDEP2 cell line and detected the phenotype. The results are presented in Supplementary Figure 9 in the revised manuscript. As shown in Supplementary Figure 9A, IDH1 deficiency resulted in reduced cell number in HUDEP2 cells, a phenotype that was rescued by overexpression of wild-type IDH1 but not by NES-IDH1. Given IDH1's well-established role in redox homeostasis through catalyzing isocitrate to α-KG conversion, we hypothesized that both wild-type IDH1 and NES-IDH1 overexpression would significantly restore α-KG levels compared to the IDH1-deficient group. Supplementary Figure 9B demonstrates that IDH1 depletion resulted in a dramatic decrease in α-KG levels, whereas overexpression of either wild-type IDH1 or NES-IDH1 almost completely restored α-KG levels, as anticipated. These results suggest that wild-type IDH1 overexpression can restore metabolic regulatory functions as effectively as NES-IDH1 overexpression. To investigate whether apoptosis contributes to the impaired cell expansion caused by IDH1 deficiency, we performed Annexin V/PI staining to quantify apoptotic cells. As shown in Supplementary Figure 9C and D, flow cytometry analysis revealed no significant changes in apoptosis rates following either IDH1 depletion or ectopic expression of wild-type IDH1 or NES-IDH1 in IDH1 deficient HUDEP2 cells.

Flow cytometric analysis demonstrated that IDH1 deficiency triggered S-phase accumulation at day 8, indicative of cell cycle arrest. Whereas ectopic expression of wild-type IDH1 significantly rescued this cell cycle defect, overexpression of NES-IDH1 failed to ameliorate the S-phase accumulation phenotype induced by IDH1 depletion, as presented in Supplementary Figure 9E and F. Although NES-IDH1 overexpression rescued metabolic regulatory function defect, it failed to alleviate the cell cycle arrest induced by IDH1 deficiency. In contrast, wild-type IDH1 overexpression fully restored normal cell cycle progression. This functional dichotomy demonstrates that nuclear-localized IDH1 executes critical roles distinct from its cytoplasmic counterpart, and overexpression of wild-type IDH1 could efficient restore the functional impairment induced by depletion of nuclear localized IDH1.

(2) Considering the nuclear knockout of IDH1 (Sg-NES-IDH1 referenced in the previous point) is a key experimental system that the authors have employed to delineate non-metabolic functions of IDH1 in human erythropoiesis, some critical experiments are lacking to make convincing inferences.

A) The authors rely on IF to show the nuclear deletion of Sg-NES-IDH1 HUDEP2 cells. As mentioned earlier since a knockout control is missing in IF experiments, a cellular fractionation experiment (similar to what is shown in Figure 2F) is required to convincingly show the nuclear deletion in these cells.

We sincerely thank the reviewer for raising this critical point. As suggested, we have performed additional IF experiments and cellular fractionation experiments to comprehensively address the subcellular localization of IDH1.

The results of IF staining were shown in Figure 3C of the revised manuscript. In Control HUDEP2 cells, endogenous IDH1 was detected in both the cytoplasm and nucleus. This dual localization may reflect its dynamic roles in cytoplasmic metabolic processes and potential nuclear functions under specific conditions. In Sg-IDH1 cells (IDH1 knockout), IDH1 signal was undetectable, confirming efficient depletion of the protein. In Sg-NES-IDH1 cells (overexpressing NES-IDH1 in IDH1 deficient cells), IDH1 predominantly accumulated in the cytoplasm, consistent with the disruption of its nuclear export signal. The dual localization of IDH1 that was determined by IF staining experiment were then further confirmed by cellular fractionation assays, as shown in Figure 3D.

B) Since the authors attribute nuclear localization to a lack of metabolic/enzymatic functions, it is important to show the status of ROS and alpha-KG in the Sg-NES-IDH1 in comparison to control, wild type rescue, and knockout HUDEP2 cells. The authors observe an increase of ROS and a decrease of alpha-KG upon IDH1 knockdown. If nuclear IDH1 is not involved in metabolic functions, is there only a minimal or no impact of the nuclear knockout of IDH1 on ROS and alpha-KG, in comparison to complete knockout? These studies are lacking.

We appreciate the insightful suggestions of the reviewers and agree that the detection of ROS and alpha-KG is useful for the demonstration of the non-canonical function of IDH1. We examined alpha-KG concentrations in control, IDH1 knockout and nuclear IDH1 knockout HUDEP2 cell lines. The results showed a significant decrease in alpha-KG content after complete knockout of IDH1, whereas there was no significant change in nuclear knockout IDH1 (Supplementary Figure 9B). As to the detection of ROS level, the commercial ROS assay kits that we can get are detected using PE (Excitation: 565nm; Emission: 575nm) and FITC (Excitation: 488nm; Emission: 518nm) channels in flow cytometry. We constructed HUDEP2 cell lines of Sg-IDH1 and Sg-NES-IDH1 to express green fluorescent protein (Excitation: 488nm; Emission: 507nm) and Kusabira Orange fluorescent protein (Excitation: 500nm; Emission: 561nm) by themselves. Unfortunately, due to the spectral overlap of the fluorescence channels, we were unable to detect the changes in ROS levels in these HUDEP2 cell lines using the available commercial kit.

(3) The authors report abnormal nuclear phenotype in IDH1 deficient erythroid cells. It is not clear what parameters are used here to define and quantify abnormal nuclei. Based on the cytospins (eg., Figure 1A, 3D) many multinucleated cells are seen in both shIDH1 and Sg-NES-IDH1 erythroid cells, compared to control cells. Importantly, this phenotype and enucleation defects are not rescued by the administration of alpha-KG (Figures 1E, F). The authors study these nuclei with electron microscopy and report increased euchromatin in Figure 4B. However, there is no discussion or quantification of polyploidy/multinucleation in the IDH1 deficient cells, despite their increased presence in the cytospins.

A) PI staining followed by cell cycle FACS will be helpful in gauging the extent of polyploidy in IDH1 deficient cells and could add to the discussions of the defects related to abnormal nuclei.

We appreciate the reviewer’s insightful suggestion. Since PI dye is detected using the PE channel (Excitation: 565nm; Emission: 575nm) of the flow cytometer and the HUDEP2 cell line expresses Kusabira orange fluorescent protein (Excitation: 500nm; Emission: 561nm), we were unable to use PI staining to detect the cell cycle. Edu staining is another commonly used method to determine cell cycle progression, and we performed Edu staining followed by flow cytometry analysis on Control, Sg-IDH1 and Sg-NES-IDH1 HUDEP2 cells, respectively. The results showed that complete knockdown of IDH1 resulted in S-phase block and increased polyploidy in HUDEP2 cells on day 8 of erythroid differentiation, and overexpression of IDH1-NES did not reverse this phenotype (Supplemental Figure 9E-F). Moreover, we have added a discussion of abnormal nuclei being associated with impaired erythropoiesis.

B) For electron microscopy quantification in Figures 4B and C, how the quantification was done and the labelling of the y-axis (% of euchromatin and heterochromatin) in Figure 4 C is not clear and is confusingly presented. The details on how the quantification was done and a clear label (y-axis in Figure 4C) for the quantification are needed.

Thanks for the reviewer's suggestion. In this study, we calculated the area of nuclear, heterochromatin and euchromatin by using Image J software. We addressed the quantification strategy in the section of Supplementary methods of the revised Supplementary file. In addition, the y-axis label in Figure 4C was changed to “the area percentage of euchromatin and heterochromatin’’.

C) As mentioned earlier, what parameters were used to define and quantify abnormal nuclei (e.g. Figure 1A) needs to be discussed clearly. The red arrows in Figure 1A all point to bi/multinucleated cells. If this is the case, this needs to be made clear.

We thank the reviewer for their suggestion. In our present study, nuclear malformations were defined as cells exhibiting binucleation or multinucleation based on cytospin analysis. A minimum of 300 cells per group were evaluated, and the proportion of aberrant nuclei was calculated as (number of abnormal cells / total counted cells) × 100%.

(4) The authors mention that their previous study (reference #22) showed that ROS scavengers did not rescue dyseythropoiesis in shIDH1 cells. However, in this referenced study they did report that vitamin C, a ROS scavenger, partially rescued enucleation in IDH1 deficient cells and completely suppressed abnormal nuclei in both control and IDH1 deficient cells, in addition to restoring redox homeostasis by scavenging reactive oxygen species in shIDH1 erythroid cells. In the current study, the authors used ROS scavengers GSH and NAC in shIDH1 erythroid cells and showed that they do not rescue abnormal nuclei phenotype and enucleation defects. The differences between the results in their previous study with vitamin C vs GSH and NAC in the context of IDH1 deficiency need to be discussed.

We appreciate the reviewer’s insightful observation. The apparent discrepancy between the effects of vitamin C (VC) in our previous study and glutathione (GSH)/N-acetylcysteine (NAC) in the current work can be attributed to divergent molecular mechanisms beyond ROS scavenging. A growing body of evidence has identified vitamin C as a multifunctional regulator. In addition to acting as an antioxidant maintaining redox homeostasis, VC also acts as a critical epigenetic modulator. VC have been identified as a cofactor for α-ketoglutarate (α-KG)-dependent dioxygenases, including TET2, which catalyzes 5-methylcytosine (5mC) oxidation to 5-hydroxymethylcytosine (5hmC) [1,2]. Structural studies confirm its direct interaction with TET2’s catalytic domain to enhance enzymatic activity in vitro [3]. The biological significance of the epigenetic modulation induced by vitamin C is illustrated by its ability to improve the generation of induced pluripotent stem cells and to induce a blastocyst-like state in mouse embryonic stem cells by promoting demethylation of H3K9 and 5mC, respectively [4,5]. In contrast, GSH and NAC are canonical ROS scavengers lacking intrinsic epigenetic-modifying activity. While they effectively neutralize oxidative stress (as validated by reduced ROS levels in our current data, Supplemental Figure 7), their inability to rescue nuclear abnormalities or enucleation defects in IDH1 deficient cells suggests that IDH1 deficiency-driven dyserythropoiesis is not solely ROS-dependent.

References:

(1) Blaschke K, Ebata KT, Karimi MM, Zepeda-Martínez JA, Goyal P, et al. Vitamin C induces Tet-dependent DNA demethylation and a blastocyst-like state in ES cells. Nature. 20138;500(7461): 222-226.

(2) Minor EA, Court BL, Young JI, Wang G. Ascorbate induces ten-eleven translocation (Tet) methylcytosine dioxygenase-mediated generation of 5-hydroxymethylcytosine. J Biol Chem. 2013;288(19): 13669-13674.

(3) Yin R, Mao S, Zhao B, Chong Z, Yang Y, et al. Ascorbic acid enhances Tet-mediated 5-methylcytosine oxidation and promotes DNA demethylation in mammals. J Am Chem Soc. 2013;135(28):10396-10403.

(4) Esteban MA, Wang T, Qin B, Yang J, Qin D, et al. Vitamin C enhances the generation of mouse and human induced pluripotent stem cells. Cell Stem Cell. 2010;6(1):71-79.

(5) Chung T, Brena RM, Kolle G, Grimmond SM, Berman BP, et al. Vitamin C promotes widespread yet specific DNA demethylation of the epigenome in human embryonic stem cells. Stem Cells. 2010;28(10):1848-1855.

(5) The authors describe an increase in euchromatin as the consequential abnormal nuclei phenotype in shIDH1 erythroid cells. However, in their RNA-seq, they observe an almost equal number of genes that are up and down-regulated in shIDH1 cells compared to control cells. If possible, an RNA-Seq in nuclear knockout Sg-NES-IDH1 erythroid cells in comparison with knockout and wild-type cells will be helpful to tease out whether a specific absence of IDH1 in the nucleus (ie., lack of metabolic functions of IDH) impacts gene expression differently.

Thanks for the reviewer's suggestion. ATAC-seq showed an increase in chromatin accessibility after IDH1 deletion, but the number of up-regulated genes was slightly larger than that of down-regulated genes, which may be caused by the metabolic changes affected by IDH1 deletion. In order to explore the effect of chromatin accessibility changes on gene expression after IDH1 deletion, we analyzed the changes in differential gene expression at the differential ATAC peak region (as shown in Author response image 1), and the results showed that the gene expression at the ATAC peak region with increased chromatin accessibility was significantly up-regulated. This may explain the regulation of chromatin accessibility on gene expression.

Author response image 1.

Box plots of gene expression differences of differential ATAC peaks located in promoter for the signal increasing and decreasing groups.

(6) In Figure 8, the authors show data related to SIRT1's role in mediating non-metabolic, chromatin-associated functions of IDH1.

A) The authors show that SIRT1 inhibition leads to a rescue of enucleation and abnormal nuclei. However, whether this rescues the progression through the late stages of terminal differentiation and the euchromatin/heterochromatin ratio is not clear.

Thanks for the reviewer's suggestion. As shown in Supplementary Figure 14 and 15 in the revised Supplementary Data, our data showed that both the treatment of SRT1720 on normal erythroid cells and treatment of IDH1-deficient erythroid cells with SIRT1 inhibitor both have no effect on the terminal differentiation.

(7) In Figure 4 and Supplemental Figure 8, the authors show the accumulation and altered cellular localization of H3K79me3, H3K9me3, and H3K27me2, and the lack of accumulation of other three histone modifications they tested (H3K4me3, H3K35me4, and H3K36me2) in shIDH1 cells. They also show the accumulation and altered localization of the specific histone marks in Sg-NES-IDH1 HUDEP2 cells.

A) To aid better comparison of these histone modifications, it will be helpful to show the cell fractionation data of the three histone modifications that did not accumulate (H3K4me3, H3K35me4, and H3K36me2), similar to what was shown in Figure 4E for H3K79me3, H3K9me3, and H3K27me2).

We appreciate the reviewer’s insightful suggestion. We collected erythroblasts on day 15 of differentiation from cord blood-derived CD34⁺ hematopoietic stem cells to erythroid lineage and performed ChIP assay. As shown in Author response image 2, the results showed that the concentration of bound DNA of H3K9me3, H3K27me2 and H3K79me3 was too low to meet the sequencing quality requirement, which was consistent with that of WB. In addition, we tried to perform ChIP-seq for H3K79me3, and the results showed that there was no marked peak signal.

Author response image 2.

ChIP-seq analysis show that there was no marked peak signal of H3K79me3 on D15. (A) Quality control of ChIP assay for H3K9me3, H3K27me2, and H3K79me3. (B) Representative peaks chart image showed normalized ChIP signal of H3K79me3 at gene body regions. (C) Heatmaps displayed normalized ChIP signal of H3K79me3 at gene body regions. The window represents ±1.5 kb regions from the gene body. TES, transcriptional end site; TSS, transcriptional start site.

C) Among the three histone marks that are dysregulated in IDH1 deficient cells (H3K79me3, H3K9me3, and H3K27me2), the authors show via ChIP-seq (Fig5) that H3K79me3 is the critical factor. However, the ChIP-seq data shown here lacks many details and this makes it hard to interpret the data. For example, in Figure 5A, they do not mention which samples the data shown correspond to (are these differential peaks in shIDH1 compared to shLuc cells?). There is also no mention of how many replicates were used for the ChIP seq studies.

We thank the reviewer for pointing this out. We apologize for not clearly describing the ChIP-seq data for H3K9me3, H3K27me2 and H3K79me3 and we have revised them in the corresponding paragraphs. Since H3 proteins gradually translocate from the nucleus to the cytoplasm starting at day 11 (late Baso-E/Ploy-E) of erythroid lineage differentiation, we performed ChIP-seq for H3K9me3, H3K27me2 and H3K79me3 only for the shIDH1 group, and set up three independent biological replicates for each of them.

Reviewer #2 (Public Review):

Li and colleagues investigate the enzymatic activity-independent function of IDH1 in regulating erythropoiesis. This manuscript reveals that IDH1 deficiency in the nucleus leads to the redistribution of histone marks (especially H3K79me3) and chromatin state reprogramming. Their findings suggest a non-typical localization and function of the metabolic enzyme, providing new insights for further studies into the non-metabolic roles of metabolic enzymes. However, there are still some issues that need addressing:

(1) Could the authors show the RNA and protein expression levels (without fractionation) of IDH1 on different days throughout the human CD34+ erythroid differentiation?

We sincerely appreciate the reviewer’s constructive feedback. To address this point, we have now systematically quantified IDH1 expression dynamics across erythropoiesis stages using qRT-PCR and Western blot analyses. As quantified in Supplementary fige 1, IDH1 expression exhibited a progressive upregulation during early erythropoiesis and subsequently stabilized throughout terminal differentiation.

(2) Even though the human CD34+ erythroid differentiation protocol was published and cited in the manuscript, it would be helpful to specify which erythroid stages correspond to cells on days 7, 9, 11, 13, and 15.

We sincerely thank the reviewer for raising this important methodological consideration. Our research group has previously established a robust platform for staged human erythropoiesis characterization using cord blood-derived CD34⁺ hematopoietic stem cells (HSCs) [6-9]. This standardized protocol enables high-purity isolation and functional analysis of erythroblasts at defined differentiation stages.

Thanks for the reviewer’s suggestion. Our previous work (Jingping Hu et.al, Blood 2013. Xu Han et.al, Blood 2017.Yaomei Wang et.al, Blood 2021.) have isolation and functional characterization of human erythroblasts at distinct stages by using Cord blood. These works illustrated that using cord blood-derived hematopoietic stem cells and purification each stage of human erythrocytes can facilitate a comprehensive cellular and molecular characterization.

Following isolation from cord blood, CD34⁺ cells were cultured in a serum-free medium and induced to undergo erythroid differentiation using our standardized protocol. The process of erythropoiesis was comprised of 2 phases. During the early phase (day 0 to day 6), hematopoietic stem progenitor cells expanded and differentiated into erythroid progenitors, including BFU-E and CFU-E cells.

During terminal erythroid maturation (day 7 to day 15), CFU-E cells progressively transitioned through defined erythroblast stages, as validated by daily cytospin morphology and expression of band 3/α4 integrin. The stage-specific composition was quantitatively characterized as follows:

Author response table 1.

The composition of erythroblast during terminal stage erythropoiesis.

This differentiation progression from proerythroblasts (Pro-E) through basophilic (Baso-E), polychromatic (Poly-E), to orthochromatic erythroblasts (Ortho-E) recapitulates physiological human erythropoiesis, confirming the validity of our differentiation system for mechanistic studies.

Reference:

(6) Li J, Hale J, Bhagia P, Xue F, Chen L, et al. Isolation and transcriptome analyses of human erythroid progenitors: BFU-E and CFU-E. Blood. 2014;124(24):3636-3645.

(7) Hu J, Liu J, Xue F, Halverson G, Reid M, et al. Isolation and functional characterization of human erythroblasts at distinct stages: implications for understanding of normal and disordered erythropoiesis in vivo. Blood. 2013;121(16):3246-3253.

(8) Wang Y, Li W, Schulz VP, Zhao H, Qu X, et al. Impairment of human terminal erythroid differentiation by histone deacetylase 5 deficiency. Blood. 2021;138(17):1615-1627.

(9) Li M, Liu D, Xue F, Zhang H, Yang Q, et al. Stage-specific dual function: EZH2 regulates human erythropoiesis by eliciting histone and non-histone methylation. Haematologica. 2023;108(9):2487-2502.

(3) It is important to mention on which day the lentiviral knockdown of IDH1 was performed. Will the phenotype differ if the knockdown is performed in early vs. late erythropoiesis? In Figures 1C and 1D, on which day do the authors begin the knockdown of IDH1 and administer NAC and GSH treatments?

We sincerely appreciate the reviewer’s inquiry regarding the experimental timeline. The day of getting CD34⁺ cells was recorded as day 0. Lentivirus of IDH1-shRNA and Luciferase -shRNA was transduced in human CD34⁺ at day 2. Puromycin selection was initiated 24h post-transduction to eliminate non-transduced cells. IDH1-KD cells were then selected for 3 days. The knock down deficiency of IDH1 was determined on day 7. NAC or GSH was added to culture medium and replenished every 2 days.

(4) While the cell phenotype of IDH1 deficiency is quite dramatic, yielding cells with larger nuclei and multi-nuclei, the authors only attribute this phenotype to defects in chromatin condensation. Is it possible that IDH1-knockdown cells also exhibit primary defects in mitosis/cytokinesis (not just secondary to the nuclear condensation defect)?), given the function of H3K79Me in cell cycle regulation?

We appreciate the reviewer’s insightful suggestion. We performed Edu based cell cycle analysis on Control, Sg-IDH1 and Sg-NES-IDH1 HUDEP2 cells, respectively. The results showed that IDH1 deficiency resulted in S-phase block and increased polyploidy in HUDEP2 cells on day 8 of erythroid differentiation. NES-IDH1 overexpression failed to rescue these defects, indicating nuclear IDH1 depletion as the primary driving factor (Figure 3E,F). Recent studies have established a clear link between cell cycle arrest and nuclear malformation. Chromosome mis-segregation, nuclear lamina disruption, mechanical stress on the nuclear envelope, and nucleolar dysfunction all contribute to nuclear abnormalities that trigger cell cycle checkpoints [10,11]. Based on all these findings, it reasonable for us to speculate that the cell cycle defect in IDH1 deficient cells might caused by the nuclear malfunction.

Reference:

(10) Hong T, Hogger AC, Wang D, Pan Q, Gansel J, et al. Cell Death Discov. CDK4/6 inhibition initiates cell cycle arrest by nuclear translocation of RB and induces a multistep molecular response. 2024;10(1):453.

(11) Hervé S, Scelfo A, Marchisio GB, Grison M, Vaidžiulytė K, et al. Chromosome mis-segregation triggers cell cycle arrest through a mechanosensitive nuclear envelope checkpoint. Nat Cell Biol. 2025;27(1):73-86. 

(5) Why are there two bands of Histone H3 in Figure 4A?

We sincerely appreciate the reviewer's insightful observation regarding the dual bands of Histone H3 in our original Figure 4A. Upon rigorous investigation, we identified that the observed doublet pattern likely originated from the inter-batch variability of the original commercial antibody. To conclusively resolve this technical artifact, we have procured a new lot of Histone H3 antibody and repeated the western blot experimental under optimized conditions, and the results demonstrates a single band of H3.

(6) Displaying a heatmap and profile plots in Figure 5A between control and IDH1-deficient cells will help illustrate changes in H3K79me3 density in the nucleus after IDH1 knockdown.

Thank you for your suggestion. As presented in Author response image 2, we performed ChIP assays on erythroblasts collected at day 15. However, the concentration of H3K79me3-bound DNA was insufficient to meet the quality threshold required for reliable sequencing. Consequently, we are unable to generate the requested heatmap and profile plots due to limitations in data integrity from this experimental condition.

Reviewer #3 (Public Review):

Li, Zhang, Wu, and colleagues describe a new role for nuclear IDH1 in erythroid differentiation independent from its enzymatic function. IDH1 depletion results in a terminal erythroid differentiation defect with polychromatic and orthochromatic erythroblasts showing abnormal nuclei, nuclear condensation defects, and an increased proportion of euchromatin, as well as enucleation defects. Using ChIP-seq for the histone modifications H3K79me3, H3K27me2, and H3K9me3, as well as ATAC-seq and RNA-seq in primary CD34-derived erythroblasts, the authors elucidate SIRT1 as a key dysregulated gene that is upregulated upon IDH1 knockdown. They furthermore show that chemical inhibition of SIRT1 partially rescues the abnormal nuclear morphology and enucleation defect during IDH1-deficient erythroid differentiation. The phenotype of delayed erythroid maturation and enucleation upon IDH1 shRNA-mediated knockdown was described in the group's previous co-authored study (PMID: 33535038). The authors' new hypothesis of an enzyme- and metabolism-independent role of IDH1 in this process is currently not supported by conclusive experimental evidence as discussed in more detail further below. On the other hand, while the dependency of IDH1 mutant cells on NAD+, as well as cell survival benefit upon SIRT1 inhibition, has already been shown (see, e.g, PMID: 26678339, PMID: 32710757), previous studies focused on cancer cell lines and did not look at a developmental differentiation process, which makes this study interesting.

(1) The central hypothesis that IDH1 has a role independent of its enzymatic function is interesting but not supported by the experiments. One of the author's supporting arguments for their claim is that alpha-ketoglutarate (aKG) does not rescue the IDH1 phenotype of reduced enucleation. However, in the group's previous co-authored study (PMID: 33535038), they show that when IDH1 is knocked down, the addition of aKG even exacerbates the reduced enucleation phenotype, which could indicate that aKG catalysis by cytoplasmic IDH1 enzyme is important during terminal erythroid differentiation. A definitive experiment to test the requirement of IDH1's enzymatic function in erythropoiesis would be to knock down/out IDH1 and re-express an IDH1 catalytic site mutant. The authors perform an interesting genetic manipulation in HUDEP-2 cells to address a nucleus-specific role of IDH1 through CRISPR/Cas-mediated IDH1 knockout followed by overexpression of an IDH1 construct containing a nuclear export signal. However, this system is only used to show nuclear abnormalities and (not quantified) accumulation of H3K79me3 upon nuclear exclusion of IDH1. Otherwise, a global IDH1 shRNA knockdown approach is employed, which will affect both forms of IDH1, cytoplasmic and nuclear. In this system and even the NES-IDH1 system, an enzymatic role of IDH1 cannot be excluded because (1) shRNA selection takes several days, prohibiting the assessment of direct effects of IDH1 loss of function (only a degron approach could address this if IDH1's half-life is short), and (2) metabolic activity of this part of the TCA cycle in the nucleus has recently been demonstrated (PMID: 36044572), and thus even a nuclear role of IDH1 could be linked to its enzymatic function, which makes it a challenging task to separate two functions if they exist.

We appreciate the reviewer’s emphasis on rigorously distinguishing between enzymatic and enzymatic independent roles of IDH1. In our revised manuscript, we have removed all assertions of a "metabolism-independent" mechanism. Instead, we focus on demonstrating that nuclear-localized IDH1 contributes to chromatin state regulation during terminal erythropoiesis (e.g., H3K79me3 accumulation). While we acknowledge that nuclear IDH1’s enzymatic activity may still play a role [12], our data emphasize its spatial association with chromatin remodeling. We now explicitly state that nuclear IDH1’s function may involve both enzymatic and structural roles, and further studies are required to dissect these mechanisms.

Reference:

(12) Kafkia E, Andres-Pons A, Ganter K, Seiler M, Smith TS, et al.Operation of a TCA cycle subnetwork in the mammalian nucleus. Sci Adv. 2022;8(35):eabq5206.

(2) It is not clear how the enrichment of H3K9me3, a prominent marker of heterochromatin, upon IDH1 knockdown in the primary erythroid culture (Figure 4), goes along with a 2-3-fold increase in euchromatin. Furthermore, in the immunofluorescence (IF) experiments presented in Figure 4Db, it seems that H3K9me3 levels decrease in intensity (the signal seems more diffuse), which seems to contrast the ChIP-seq data. It would be interesting to test for localization of other heterochromatin marks such as HP1gamma. As a related point, it is not clear at what stage of erythroid differentiation the ATAC-seq was performed upon luciferase- and IDH1-shRNA-mediated knockdown shown in Figure 6. If it was done at a similar stage (Day 15) as the electron microscopy in Figure 4B, then the authors should explain the discrepancy between the vast increase in euchromatin and the rather small increase in ATAC-seq signal upon IDH1 knockdown.

Thank you for raising this important point. We agree that while H3K9me3 and H3K27me2 modifications are detectable in the nucleus, their functional association with chromatin in this context remains unclear. Our ChIP-seq data did not reveal distinct enrichment peaks for H3K9me3 or H3K27me2 (unlike the well-defined H3K79me3 peaks), suggesting that these marks may not be stably bound to specific chromatin regions under the experimental conditions tested. However, we acknowledge that the absence of clear peaks in our dataset does not definitively rule out chromatin interactions, as technical limitations or transient binding dynamics could influence these results. To avoid over-interpretation, we have removed speculative statements about the chromatin-unbound status of H3K9me3 and H3K27me2 from the revised manuscript. This revision aligns with our broader effort to present conclusions strictly supported by the current data while highlighting open questions for future investigation.

(3)The subcellular localization of IDH1, in particular its presence on chromatin, is not convincing in light of histone H3 being enriched in the cytoplasm on the same Western blot. H3 would be expected to be mostly localized to the chromatin fraction (see, e.g., PMID: 31408165 that the authors cite). The same issue is seen in Figure 4A.

We sincerely appreciate the reviewer's insightful comment regarding the subcellular distribution of histone H3 in our study. We agree that histone H3 is classically associated with chromatin-bound fractions, and its cytoplasmic enrichment in our Western blot analyses appears counterintuitive at first glance. However, this observation is fully consistent with the unique biology of terminal erythroid differentiation, which involves drastic nuclear remodeling and histone release - a hallmark of terminal stage erythropoiesis. Terminal erythroid differentiation is characterized by progressive nuclear condensation, chromatin compaction, and eventual enucleation. During this phase, global chromatin reorganization leads to the active eviction of histones from the condensed nucleus into the cytoplasm. This process has been extensively documented in erythroid cells, with studies demonstrating cytoplasmic accumulation of histones H3 and H4 as a direct consequence of nuclear envelope breakdown and chromatin decondensation preceding enucleation [13-16]. Our experiments specifically analyzed terminal-stage polychromatic and orthochromatic erythroblasts. At this stage, histone releasing into the cytoplasm is a dominant biological event, explaining the pronounced cytoplasmic H3 signal in our subcellular fractionation assays.

In summary, the cytoplasmic enrichment of histone H3 in our data aligns with established principles of erythroid biology and reinforces the physiological relevance of our findings. We thank the reviewer for raising this critical point, which allowed us to better articulate the unique aspects of our experimental system.

Reference:

(13) Hattangadi SM, Martinez-Morilla S, Patterson HC, Shi J, Burke K, et al. Histones to the cytosol: exportin 7 is essential for normal terminal erythroid nuclear maturation. Blood. 2014;124(12):1931-1940.

(14) Zhao B, Mei Y, Schipma MJ, Roth EW, Bleher R, et al. Nuclear Condensation during Mouse Erythropoiesis Requires Caspase-3-Mediated Nuclear Opening. Dev Cell. 2016;36(5): 498-510.

(15) Zhao B, Liu H, Mei Y, Liu Y, Han X, et al. Disruption of erythroid nuclear opening and histone release in myelodysplastic syndromes. Cancer Med. 2019;8(3):1169-1174. 

(16) Zhen R, Moo C, Zhao Z, Chen M, Feng H, et al.  Wdr26 regulates nuclear condensation in developing erythroblasts. Blood. 2020;135(3):208-219.

(4) This manuscript will highly benefit from more precise and complete explanations of the experiments performed, the material and methods used, and the results presented. At times, the wording is confusing. As an example, one of the "Key points" is described as "Dyserythropoiesis is caused by downregulation of SIRT1 induced by H3K79me3 accumulation." It should probably read "upregulation of SIRT1".

We sincerely thank the reviewer for highlighting the need for improved clarity in our experimental descriptions and textual precision. We fully agree that rigorous wording is essential to accurately convey scientific findings. Specific modifications have been made and are highlighted in Track Changes mode in the resubmitted manuscript.

The reviewer correctly identified an inconsistency in the original phrasing of one key finding. The sentence in question ("Dyserythropoiesis is caused by downregulation of SIRT1 induced by H3K79me3 accumulation") has been revised to:"Dyserythropoiesis is caused by the upregulation of SIRT1 mediated through H3K79me3 accumulation." This correction aligns with our experimental data showing that H3K79me3 elevation promotes SIRT1 transcriptional activation. We apologize for this oversight and have verified the consistency of all regulatory claims in the text.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) It will be helpful to mention/introduce the cells used for the study at the beginning of the results section. For example, for Figure 1A neither the figure legend nor the results text includes information on the cells used.

Thanks for the reviewer’s suggestion. The detail information of the cells that were used in our study have been provided in the revised manuscript.

(2) Important details for many figures are lacking. For example, in Figure 5, there is no mention of the replicates for ChIP-Seq studies. Also, the criteria used for quantifications of abnormal nuclei, % euchromatin vs heterochromatin, the numbers of biological replicates, and how many fields/cells were used for these quantifications are missing.

We thank the reviewer for emphasizing the importance of methodological transparency. It has been revised accordingly. The ChIP-Seq data in Figure 5 was generated from three independent biological replicates to ensure reproducibility. In this study, Image J software was used to calculate the area of nuclear, heterochromatin/euchromatin and to quantify the percentage of euchromatin and heterochromatin. A minimum of 300 cells per group were evaluated, and the proportion of aberrant nuclei was calculated as (number of abnormal cells / total counted cells) × 100%.

(3) It will be helpful if supplemental data are ordered according to how they are discussed in the text. Currently, the order of the supplemental data is hard to keep track of eg., the results section starts describing supplemental Figure 1, then the text jumps to supplemental Figure 5 followed by Supplemental Figure 3 (and so on).

Thanks for the reviewer’s suggestion. It has been revised accordingly.

(4) Overall, there are many incomplete sentences and typos throughout the manuscript including some of the figures e.g. on page 10 the sentence "Since the generation of erythroid with abnormal nucleus and reduction of mature red blood cells caused by IDH1 absence are notable characteristics of MDS and AML." is incomplete. On page 11, it reads "Histone post-modifications". This needs to be either histone modifications or histone post-translational modifications. In Figure 4C, the y-axis title is hard to understand "% of euchromatin and heterochromatin". Overall, the document needs to be proofread and revised carefully.

Thanks for the reviewer’s suggestion. We have made revision accordingly in the revised manuscript. The sentence "Since the generation of erythroid with abnormal nucleus and reduction of mature red blood cells caused by IDH1 absence are notable characteristics of MDS and AML." has been revised to “The production of erythrocytes with abnormal nuclei and the reduction of mature erythrocytes due to IDH1 deletion are prominent features of MDS and AML.”  “% of euchromatin and heterochromatin” has been modified to “Area ratio of euchromatin to heterochromatin”.

Reviewer #3 (Recommendations For The Authors):

The following critique points aim to help the authors to improve their manuscript:

(1) The authors reason (p. 10) that because mutant IDH1 has been shown to result in altered chromatin organization, this could be the case in their system, too. However, mutant IDH1 has an ascribed metabolic consequence, the generation of 2-HG, which further weakens the author's argument for an enzymatically independent role of IDH1 in their system. The same is true for the author's observation in Supplementary Figure 9B that in IDH1-mutant AML/MDS samples, H3K79me3 colocalized with the IDH1 mutants in the nucleus. Again, this speaks in favor of IDH1's role being linked to metabolism. The authors could re-write this manuscript, not so much emphasizing the separation of function between different subcellular forms of IDH1 but rather focusing on the chromatin changes and how they could be linked to the actual phenotype, the nuclear condensation and enucleation defect - if so, addressing the surprising finding of enrichment of both active and repressive chromatin marks will be important.

Thanks for the reviewer’s suggestion. We agree with the reviewers and editors all the data we present in the current are not robust enough to rigorously distinguish between enzymatic and enzymatic-independent roles of IDH1. In our revised manuscript, we have removed all assertions of a "metabolism-independent" mechanism. Instead, we focus on demonstrating that nuclear-localized IDH1 contributes to chromatin state regulation during terminal erythropoiesis (e.g., H3K79me3 accumulation).

(2) How come so many genes were downregulated by RNA-seq (about an equal number as upregulated genes) but not more open by ATAC-seq? The authors should discuss this result.

Thanks for the reviewer's suggestion. ATAC-seq showed an increase in chromatin accessibility after IDH1 deletion, but the number of up-regulated genes was slightly larger than that of down-regulated genes, which may be caused by the metabolic changes affected by IDH1 deletion. In order to explore the effect of chromatin accessibility changes on gene expression after IDH1 deletion, we analyzed the changes in differential gene expression at the differential ATAC peak region (as shown in the figure below), and the results showed that the gene expression at the ATAC peak region with increased chromatin accessibility was significantly up-regulated. This may explain the regulation of chromatin accessibility on gene expression.

(3) For the ChIP-seq analyses of H3K79me3, H3K27me2, and H3K9me3, the authors should not just show genome-wide data but also several example gene tracks to demonstrate the differential abundance of peaks in control versus IDH1 knockdown. Furthermore, the heatmap shown in Figure 5A should include broader regions spanning the gene bodies, to visualize the intergenic H3K27me2 and H3K9me3 peaks. Expression could very well be regulated from these intergenic regions as they could bear enhancer regions. ChIP-seq for H3K27Ac in the same setting would be very useful to identify those enhancers.

Thanks for the reviewer’s suggestion. It has been revised accordingly. We reanalyzed the ChIP-seq peak signal of H3K79me3, H3K27me2 and H3K9me3 in a wider region (±5Kb) at gene body, and the results showed that the H3K27me2 and H3K9me3 peak signals did not change significantly. Since H3K79me3 showed a higher peak signal and was mainly enriched in the promoter region, our subsequent analysis focusing on the impact of H3K79me3 accumulation on chromatin accessibility and gene expression might be more valuable.

Author response image 3.

ChIP-seq analysis show that the peak signal of H3K79me3,H3K27me2 and H3K9me3. (A) Heatmaps displayed normalized ChIP signal of H3K9me3, H3K27me2, and H3K79me3 at gene body regions. The window represents ±5 kb regions from the gene body. TES, transcriptional end site; TSS, transcriptional start site. (B) Representative peaks chart image showed normalized ChIP signal of H3K9me3, H3K27me2, and H3K79me3 at gene body regions.

(4) The absent or very mild delay (also no significance visible in the quantification plots) in the generation of orthochromatic erythroblasts on Day 13 upon IDH1 shRNA knockdown as per a4-integrin/Band3 flow cytometry does not correspond to the already quite prominent number of multinucleated cells at that stage seen by cytospin/Giemsa staining. Why do the authors think this is the case? Cytospin/Giemsa staining might be the better method to quantify this phenotype and the authors should quantify the cells at different stages in at least 100 cells from non-overlapping cytospin images.

Thanks for the reviewer’s suggestion. We have supplemented the cytpspin assay and the results were presented in Supplemental Figure 4.

(5) The pull-down assay in Figure 7E does not show a specific binding of H3K79me3 to the SIRT1 promoter. Rather, there is just more H3K79me3 in the nucleus, thus leading to generally increased binding. The authors should show that H3K79me3 does not bind more just everywhere but to specific loci. The ChIP-seq data mention only categories but don't show any gene lists that could hint at the specificity of H3K79me3 binding at genes that would promote nuclear abnormalities and enucleation defects.

We thank the reviewer for pointing this out. The GSEA results of H3K79me3 peak showed enrichment of chromatin related biological processes, and the list of associated genes is shown Figure 7B. In addition, we also displayed the changes in H3K79me3 peak signals, ATAC peak signals, and gene expression at gene loci of three chromatin-associated genes (SIRT1, KMT5A and NUCKS1).

(6) P. 12: "Representatively, gene expression levels and ATAC peak signals at SIRT1 locus were elevated in IDH1-shRNA group and were accompanied by enrichment of H3K9me3 (Figure 7F)." Figure 7F does not show an enrichment of H3K9me3, but if the authors found such, they should explain how this modification correlates with the activation of gene expression.

Thank you for bringing this issue to our attention. We sincerely apologize for the mistake in the description of Figure 7F on page 12. We have already corrected this error in the revised manuscript.

(7) Related to the mild phenotype by flow cytometry on Day 13, are the "3 independent biological replicates" from culturing and differentiating CD34 cells from 3 different donors? If all are from the same donor, experiments from at least a second donor should be performed to generalize the results.

In our current study, CD34⁺ cells were derived from different donors. 

(8) If the images in Supplementary Figure 4 are only the indicated cell type, then it is not clear how the data were quantified since only some cells in each image are pointed at and others do not seem to have as large nuclei. There is also no explanation in the legend what the colors mean (nuclei were presumably stained with DAPI, not clear what the cytoplasm stain is - GPA?).

We thank the reviewer for pointing this out. We have revised the manuscript accordingly. Specifically, the nuclei was stained with DAPI and the color was blue. The cell membrane was stained with GPA and the color was red. This staining method allows for clear visualization of the cell structure and helps to better understand the localization of the proteins of interest.

(9) It is not clear to this reviewer whether Figure 4F is a quantification of the Western Blot or of the IF data.

Figure 4F is a quantification of the Western Blot experiment.

(10) The authors sometimes do not describe experiments well, e.g., "treatment of IDH1-deficient erythroid cells with IDH1-EX527" (p. 13). EX-527 is a SIRT1 inhibitor, which the authors only explicitly mention later in that paragraph. It is unclear to this reviewer, why the authors call it IDH1-EX527.

Thank you for pointing out the unclear description in our manuscript. We apologize for the confusion caused by the unclear statement. We have revised the manuscript accordingly. The compound EX-527 is a SIRT1 inhibitor, and we have corrected the description to simply "EX-527" in the revised manuscript.

(11) The end of the introduction needs revising to be more concise; the last paragraph on p. 4 ("Recently, the decreased expression of IDH1...") partially should be integrated with the previous paragraph, and partially is repeated in the last paragraph (top paragraph on p. 5). The last sentence on p. 4, "These findings strongly suggest that aberrant expression of IDH1 is also an important factor in the pathogenesis of AML and MDS.", should rather read "increased expression of IDH1", to distinguish it from mutant IDH1 (mutant IDH1 is also aberrantly expressed IDH1).

We appreciated the reviewer for the helpful suggestion. Considering that the inclusion of this paragraph did not provide a valuable contribution to the formulation of the scientific question, we have removed it after careful consideration, and the revised manuscript is generally more logically smooth.

(12) Abstract and last sentence of the introduction: "innovative perspective" should be re-worded, as the authors present data, not a perspective. Maybe could use "evidence".

Thanks for the reviewer’s suggestion. It has been revised accordingly.

(13) "IDH1-mut AML/MDS" on p. 11. The authors should provide more information about these AML/MDS samples. The legend contains no information about them/their mutational status. How many samples did the authors look at? Do these cells contain mutations other than IDH1?

Thanks for the reviewer’s suggestion. The detail information of these AML/MDS samples are provide in supplemental table 1. In our current study, we collected ten AML/MDS samples and the majority of the samples only contain IDH1 mutations at different sites.

(14) The statement, "Taken together, these results indicated that IDH1 deficiency reshaped chromatin states and subsequently altered gene expression pattern, especially for genes regulated by H3K79me3, which was the mechanism underlying roles of IDH1 in modulation of terminal erythropoiesis." (p. 10), is not correct at that point in the manuscript as the authors have not yet introduced the RNA-seq data.

Thanks for the reviewer’s suggestion. The statement has been revised to “Taken together, these results indicated that IDH1 deficiency reshaped chromatin states by altering the abundance and distribution of H3K79me3, which was the mechanism underlying roles of IDH1 in modulation of terminal erythropoiesis”.

(15) For easier readability, the authors should present the data in order. For example, the supplemental data for IDH shRNA and siRNA should be presented together and not in Supplementary Figures 1 and 5. Supplementary Figure 3 is mentioned after Supplementary Figure 1, but before Supplementary Figure 2 - again, all data need to be presented in subsequent figures to be viewed together.

Thank you for your suggestion regarding the order of data presentation. We have reorganized the figures in the manuscript to improve readability. We apologize for any confusion caused by the previous arrangement and hope that the revised version meets your expectations.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The manuscript investigates the role of the membrane-deforming cytoskeletal regulator protein Abba in cortical development and its potential implications for microcephaly. It is a valuable contribution to the understanding of Abba's role in cortical development. The strengths and weaknesses identified in the manuscript are outlined below:

Clinical Relevance:

The authors identified a patient with microcephaly and a patient with an intellectual disability harboring a mutation in the Abba variant (R671W) adding a clinically relevant dimension to the study.

Mechanistic Insights:

The study offers valuable mechanistic insights into the development of microcephaly by elucidating the role of Abba in radial glial cell proliferation, radial fiber organization, and the migration of neuronal progenitors. The identification of Abba's involvement in the cleavage furrow during cell division, along with its interaction with Nedd9 and positive influence on RhoA activity, adds depth to our understanding of the molecular processes governing cortical development. Though the reported results establish the novel interaction between Abba and Nedd9, the authors have not addressed whether the mutant protein loses this interaction and whether that results in the observed effects.

We appreciate the reviewer’s observation and fully agree that our study does not provide direct evidence that the phenotypes induced by the R671W mutant are mediated through NEDD9. We sincerely apologize if the manuscript inadvertently conveyed this impression.

While we show that the interaction with NEDD9 plays a role in the action of ABBA, our findings suggest that NEDD9 and RhoA activation have a minor influence on the phenotypes induced by this mutation, as highlighted by the evidence we presented.

We would like to point out that we have previously addressed this point in the discussion section of the manuscript. For clarity, below is an excerpt from that section:

“heterozygous expression of the human R671W variant would exert a dominant negative effect on ABBA's role in brain development, leading to microcephaly and cognitive delay. This notion is supported by recent work disclosing additional patient carrying the R671W variant42. In the same study the significant neurological phenotypes were observed in a drosophila model where the ortholog of human MTSS2 and MTSS1 mim was deleted.   However, from a clinical genetics’ standpoint, it is unlikely to find patients with the recurrent R671W mutation without any homozygous or compound heterozygous loss-of-function mutations elsewhere in the ABBA gene. This could also suggest a gain-of-function effect of the R671W mutation. Supporting this notion, overexpressing ABBA-R671W in cells expressing the wild-type Abba in this study did not result in a dominant-negative decrease in RhoA activation, nor did it affect the expression of PH3 in vivo. These findings make it plausible to suggest that a mechanism responsible for the phenotype associated with overexpression of the human variant may primarily involve post-cell division processes, such as cell migration. “

We have made corrections to the new version of the manuscript to emphasize this further.

In Vivo Validation:

The overexpression of mutant Abba protein (R671W) resulting in phenotypic similarities to Abba knockdown effects supports the significance of Abba in cortical development.

Reviewer #2 (Public Review):

Summary:

Carabalona and colleagues investigated the role of the membrane-deforming cytoskeletal regulator protein Abba (MTSS1L/MTSS2) in cortical development to better understand the mechanisms of abnormal neural stem cell mitosis. The authors used short hairpin RNA targeting Abba20 with a fluorescent reporter coupled with in-utero electroporation of E14 mice to show changes to neural progenitors. They performed flow cytometry for in-depth cell cycle analysis of Abba-shRNA impact on neural progenitors and determined an accumulation in the S phase. Using culture rat glioma cells and live imaging from cortical organotypic slides from mice in utero electroporated with Abba-shRNA, the authors found Abba played a prominent role in cytokinesis. They then used a yeast-two-hybrid screen to identify three high-confidence interactors: Beta-Trcp2, Nedd9, and Otx2. They used immunoprecipitation experiments from E18 cortical tissue coupled with C6 cells to show Abba's requirement for Nedd9 localization to the cleavage furrow/cytokinetic bridge. The authors performed a shRNA knockdown of Nedd9 by in-utero electroporation of E14 mice and observed similar results as with the Abba-shRNA. They tested a human variant of Abba using in-utero electroporation of cDNA and found disorganized radial glial fibers and misplaced, multipolar neurons, but lacked the impact of cell division seen in the shRNA-Abba model.

Strengths:

A fundamental question in biology about the mechanics of neural stem cell division.

Directly connecting effects in Abba protein to downstream regulation of RhoA via Nedd9.

Incorporation of human mutation in ABBA gene.

Use of novel technologies in neurodevelopment and imaging.

Weaknesses:

Unexplored components of the pathway (such as what neurogenic populations are impacted by Abba mutation) and unleveraged aspects of their data (such as the live imaging) limit the scope of their findings and leave significant questions about the effect of ABBA on radial glia development.

(1) The claim of disorganized radial glial fibers lacks quantifications.

On page 11, the authors claim that knockdown of Abba leads to changes in radial glial morphology observed with vimentin staining. Here they claim misoriented apical processes, detached end feet, and decreased number of RGP cells in the VZ. However, they do not provide quantification of process orientation to better support their first claim. Measurements of radial glia fiber morphology (directionality, length) and angle of division would be metrics that can be applied to data.

In the corrected version of the manuscript, we provide new qualification of changes in dispersion of vimentin immunostaining (Supplementary Figure 1).

Some of these analyses could be done in their time-lapse microscopy images, such as to quantify the number of cell divisions during their period of analysis (though that is short-15 hours).

This is indeed a very good idea. We have reanalyzed the recordings to follow cell division. Unfortunately, the number of cells that we were able to follow was low, making statistical analysis of the data unreliable.  As the reviewer alluded in the comment longer recording times than 15h are required to make reliable conclusion. Instead, we have performed live-cell imaging using Aniling-GFP coelectroporeted with RFP as a marker of mitotic progression . We monitored the distribution of cells showing accumulation of Anillin-GFP in control (Scramble) and ABBA-shRNA3 conditions (this data was added to new Supplementary Figure 3). Anillin has been shown to be an efficient tool to monitor cell division in vivo as in particular as it displays accumulation and correlated increase intensity of Anillin-GFP ((Hesse et al Nature Com. 2012, DOI: 10.1038/ncomms2089).

(2) It is unclear where the effect is:

-In RG or neuroblasts? Is it in cell cleavage that results in the accumulation of cells at VZ (as sometimes indicated by their data like in Figure 2A or 4D)?

The data suggest that radial glial (RG) cells are indeed blocked prior to abscission. This phenomenon might contribute to the accumulation of cells at the ventricular zone (VZ), as indicated by observations such as those in Figure 2A and 4D. The interruption in cell cleavage likely prevents the proper progression of division, causing RG cells to remain at the VZ rather than proceeding with their normal differentiation or migration processes. This finding highlights a potential mechanistic link between disrupted abscission and cell accumulation in the VZ.

Interrogation of cell death (such as by cleaved caspase 3) would also help.  

Caspase-3 cleavage is widely used as a marker for apoptosis; however, it may not be the most reliable tool for monitoring apoptosis during brain cortical development. The developing brain is a highly dynamic environment where caspase-3 activation can be transient and involved in non-apoptotic processes, such as synaptic pruning and neuronal remodeling. This makes it challenging to distinguish caspase-3 activity associated with apoptosis from its roles in physiological processes.

In contrast, monitoring overall cell survival provides a more reliable measure of developmental outcomes, as it reflects the net balance of cell death and survival mechanisms. By focusing on cell survival e.g. quantification of number of RGP, we can better assess the functional consequences of apoptosis and its interplay with neurogenesis and other developmental processes.  In line with this we have added more data on the quantification of RGPC as well as their distribution in new Supplementary Figure 3. 

Given their time-lapse, can they identify what is happening to the RG fiber?

Both apical and basal endfeet appear to detach and retract prior to radial glial (RG) cell death. This is evident in Figure 1D, as well as from our observation of cellular bodies located far from the ventricular surface (VS), as demonstrated in the new Supplementary Figure 3.

The authors describe a change in "migration" but do not show evidence for this for either progenitor or neuroblast populations. Given they have nice time-lapse imaging data, could they visualize progenitor versus young neuron migration? Analysis of neuroblasts (such as with doublecortin expression in the tissue) would also help understand any issues in migration (of neurons v stem cells).

This is an excellent question that arises from the extensive data presented in this study. Addressing it would require repeating a significant portion of the experiments. We fully agree with the reviewer that these are important and obvious questions that warrant a dedicated study to answer them thoroughly. Additionally, we believe that the data showing the accumulation of migrating electroporated cells in the ventricular (V) and subventricular (SV) zones provide compelling evidence of abnormal migration in ABBA-shRNA electroporated cells.

-At cleavage furrow? In abscission? There is high-resolution data that highlights the cleavage furrow as the location of interest (Figure 3A), however, there is also data (Figure 3B) to suggest Abba is expressed elsewhere as well and there is an overall soma decrease. More detail of the localization of Abba during the division process would be helpful for example, could cleavage furrow proteins, such as Aurora B, co-localization (and potentially co-IP) help delineate subpopulations of Abba protein? Furthermore, the FRET imaging is a unique way to connect their mutation with function - could they measure/quantify differences at furrow compared to the rest of soma to further corroborate that the Abba-associated RhoA effect was furrow-enriched?

In the corrected version of the manuscript, we include new quantification of RhoA activity in the region corresponding to the cleavage furrow (New Figure 5), This new data show similar results as the previous and indicate that the changes observed are primarily derived from the cleavage furrow region. In the future a detailed dissection of the molecules involved in the mechanism would be highly desirable. These notions are now included in the discussion. 

-The data highlights nicely that a furrow doesn't clearly form when ABBA expression and subsequent RhoA activity are decreased (in Figure 3 or 5A). Does this lead to cells that can't divide because of poor abscission, especially since "rounding" still occurs? Or abnormal progenitors (with loss of fiber or inability to support neuroblast migration)? Or abnormal progression of progenitors to neuroblasts?

Our findings, combined with previous results, suggest multiple mechanisms through which ABBA depletion and subsequent Nedd9 and RhoA signaling disruptions could impact progenitor cells and neuroblasts. Below is a detailed response to each question: 

(1) Do cells fail to divide due to poor abscission?

Nedd9 is a key regulator of RhoA signaling, which could be essential for cleavage furrow ingression and abscission. Reduced Nedd9 expression may leads to non-activation of RhoA, thereby impairing cleavage furrow ingression. Furthermore, since RhoA deactivation is critical for successful abscission, any disruption in this signaling pathway could compromise the final stages of cytokinesis. While we do not directly observe failed abscission, the impaired furrow formation in Figure 3 and 5A aligns with the hypothesis that some cells may struggle to complete division due to defects in RhoA-mediated abscission. 

(2) Are abnormal progenitors generated (e.g., loss of fiber or inability to support neuroblast migration)?

Disrupted Nedd9 expression not only affects cell cycle progression but also influences the structural integrity of radial glial progenitors (RGPs). RGPs with impaired cleavage furrow ingression may exhibit detachment of apical and basal endfeet (Supplementary Figure 3), leading to abnormalities in their scaffold function. This structural disruption likely contributes to the accumulation of electroporated cells in the ventricular (V) and subventricular (SV) zones (Figure 5A), supporting the idea that abnormal progenitors fail to support proper neuroblast migration. 

(3) Is there abnormal progression of progenitors to neuroblasts?

Given that Nedd9 triggers cells to enter mitosis, its impaired function may prevent progenitors from properly progressing through the cell cycle, causing cell cycle arrest and eventual decrease survival. This would directly impact the ability of progenitors to transition into neuroblasts. Moreover, the abnormal membrane composition and PI(4,5)P2 enrichment we hypothesize during cytokinesis could disrupt ABBA recruitment and its interaction with Nedd9. This disruption would impair RhoA activation, further compromising the progression of progenitors to neuroblasts. 

In conclusion, our findings suggest that impaired ABBA expression disrupts Nedd9 and RhoA signaling, leading to poor cleavage furrow ingression, abnormal progenitor structure, and defective neuroblast migration. These processes collectively contribute to developmental defects in the cortex. Future studies focusing on live imaging of cytokinesis and cell fate mapping will help elucidate better these mechanisms further.

(3) Limited to a singular time point of mouse cortical development

On page 13, the authors outline the results of their Y2H screen with the identification of three high-confidence interactors. Notably, they used an E10.5-E12.5 mouse brain embryo library rather than one that includes E14, the age of their in-utero electroporation mice. Many of the authors' claims focus on in-utero electroporation of shRNA-Abba of E14 mice that are then evaluated at E16-18. Justification for the focus on this age range should be included to support that their findings can then be applied to all mouse corticogenesis.

We thank the reviewer to point this out. Indeed, the data suggest that the interaction between ABBA and Nedd9 occurs before E14. The reason to address the questions at E14 is that in earlier work, we have shown that ABBA is mainly expressed through E10.5-12.5 in the floorplate structure formed by radial glia. The radial glia-specific expression was confirmed through double staining with radial glial (RC2) and neuronal (Tuj1) markers at E12.5 (see Saarikangas et al. J. Cell Sci. 121:1444-1454, 2008). Thus, we consider the Y2H library relevant for identifying ABBA's interactors within radial glia. We have specified this better in the corrected manuscript.

(4) Detail of the effect of the human variant of the ABBA mutation in mice is lacking.

Their identification of the R671W mutation is interesting and the IUE model warrants more characterization, as they did with their original KD experiments.

We have now included addition data in the corrected manuscript showing R671W dependent changes in INM (Supplementary Figure 3 )

Could they show that Abba protein levels are decreased (in either cell lines or electroporated tissue)?

Estimation of ABBA expression in cell expressing ABBA R671W as in Supplemental Figure 5 did not show significant change.

-While time-lapse morphology might not have been performed, more analysis on cell division phenotype (such as plane of division and radial glia morphology) would be helpful. 

This would be indeed very informative, but we were not able to perform these analysis in the existing dataset.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Here are some suggestions for targeting some of the weaknesses by additional experiments:

Regional Demarcation in Radial Glial Cell Population:

While the authors demonstrate a decrease in overall RFP-positive cells in response to Abba knockdown, the distinction between different regions should be demarcated using cortical layer-specific markers (e.g., CUX1/BRN2 for the upper layer and CTIP2/FOXP2). Quantification based on regional markers would enhance accuracy and meaningful interpretation.

In order to harmonize the quantification during the different developmental stages we have used a broader definition of the cortical regions that may not be entirely fitting with the regions identified with the staining of Cux1 and CTIP2. We have now however included in the supplementary figure 1 with the staining for Cux1 and CTIP2 showing the corresponding regions defined in the manuscript. Supplementary Figure 1.

Mitotic Stage Marker and BrdU Staining:<br /> The discrepancy between no changes in staining with the mitotic stage marker PH3 and a reported decrease in Ki67 staining calls for further clarification. Additionally, the use of BrdU staining could distinguish the effects on dividing cells after Abba knockdown. The authors are encouraged to explore these aspects further, including their applicability to NEDD9 knockdown and Abba mutant overexpression.

As suggested by the reviewer elsewhere, we made use of life imaging. We monitored the distribution of cells showing accumulation of Anillin-GFP in control (Scramble) and ABBA-shRNA3 conditions (this data has been added to the new Supplementary Figure 3). Anillin has been shown to be an efficient tool for monitoring cell cycle stages in vivo (Hesse et al Nature Com. 2012, DOI: 10.1038/ncomms2089). Interestingly, we observed an increase in cells displaying accumulated Anillin in ABBA-shRNA3 treated cells, which is consistent with an arrest of progression of mitosis.  

Quantification of Cytokinesis Effects:

The brain slices illustrating the effects of Abba knockdown on cytokinesis would benefit from a quantification depicting changes in interkinetic nuclear migration and the number of successful mitosis events. This would enhance the clarity and interpretation of the observed effects.

In the revised manuscript we have included new data in Supplementary Figure 3 were we report the quantification of the distance of the RGC from the ventricle to address the reviewer’s comments. We were not entirely sure about comment about quantification of successful mitosis events, but as specified above, we have included new data from the monitoring of anillin. We hope to perform more detailed experiments and analysis in future studies. 

Loss of Interaction and NEDD9 Localization:

The manuscript lacks an exploration of the loss or decrease in interaction between Abba and NEDD9 in the case of the pathogenic patient-derived mutation in Abba. Addressing this aspect is crucial, as it may shed light on the underlying causes of the observed effects. Furthermore, investigating changes in NEDD9 localization following overexpression of the Abba mutant would provide additional insights.

We fully agree with the reviewer’s comment. Unfortunately the anti NEDD9 antibody had a poor performance in slice immunohistochemistry, which hampered further reliable investigation of expression and distribution changes in vivo. Resolving this issue and providing a more detailed characterization of the mechanism of Abba-NEDD9 interaction will be important in future studies.

Overall, I believe that with minor revisions and additional contextualization, the manuscript has the potential to make a significant contribution to the field. I recommend acceptance pending the incorporation of the suggested revisions.

Reviewer #2 (Recommendations For The Authors):

The manuscript is generally well-organized. We hope that given their nice experimental systems, many of the comments and questions can be addressed with their data already on hand.

Minor Comments

• For Figure 6E A closeup of the vimentin would be helpful - hard to visualize radial glia morphology at the current magnification.

This has been corrected in the new version of the manuscript

• For the in utero electroporation what was their rationale for 2-4 day interval before evaluation? For example, waiting for more cortical plate development to be able to manifest long-term effects.

We observed a massive cell death at E18, in only few of those brains we were able to still observe RFP cells. We have also tried P6 animals but none of them had significant reminding electroporated cells that’s why we have decided to focus at E17, 3 days after the electroporation to have still enough expression of the shRNA.

• Figure 4E-F lacks images of controls for comparison of effect.

This has been corrected in the revised version of the manuscript

Author response:

Reviewer #1:

The manuscript Xu et al. explores the regulation of the microtubule minus end protein CAMSAP2 localization to the Golgi by the Serine/threonine-protein kinase MARK2 (PAR1, PAR1B). The authors utilize immunofluorescence and biochemical approaches to demonstrate that MARK2 is localized at the Golgi apparatus via its spacer domain. They show that depletion of this protein alters Golgi morphology and diminishes CAMSAP2 localization to the Golgi apparatus. The authors combine mass spectroscopy and immunoprecipitation to show that CAMSAP2 is phosphorylated at S835 by MARK2, and that this phosphorylation regulates localization of CAMSAP2 at Golgi membranes. Further, the authors identify USO1 (p115) as the Golgi resident protein mediating CAMSAP2 recruitment to the Golgi apparatus following S835 phosphorylation. The authors would need to address the following queries to support their conclusions.

We sincerely thank the reviewer for their valuable time and effort in evaluating our manuscript. We deeply appreciate the constructive feedback and insightful suggestions, which have been instrumental in improving the quality and clarity of our study. We have carefully considered all the comments and have made the necessary revisions to address the concerns raised.

Major Comments 

(1) Dynamic localization of CAMSAP2 during Golgi reorientation

- The authors use fixed wound edges assays and co-localization analysis to describe changes in CAMSAP2 positioning during Golgi reorientation in response to polarizing cues (a free wound edge in this case). In Figure 1C, they present a graphical representation of quantified immunofluorescence images, using color coding to to describe the three states of Golgi reorientation in response to a wound (green, blue, red indicating non-polarised, partial and complete Golgi reorientation, respectively). They then use these 'colour coded' classifications to quantitate CAMSAP2/GM130 co-localization.It is unclear why the authors have not just used representative immunofluorescence images in the main figures. Transparent, color overlays could be placed over the cells in the representative images to indicate which of the three described states each cell is currently exhibiting. However, for clarity, I would recommend changing the color coded 'states' to a descriptor rather than a color. i.e. Figure 1D x axis labels should be 'complete' and 'partial', instead of 'red' and 'blue'. 

Thank you for this insightful suggestion. We have added representative immunofluorescence images with transparent color overlay to indicate the three Golgi orientation states. These images are included in Supplementary Figure 2B-C, providing a clear visual reference for the quantitative data. Additionally, we have revised the x-axis labels in Figure 1E from "Red" and "Blue" to "Complete" and "Partial" to ensure clarity and consistency with the descriptive terminology in the text. These changes are described in the Results section (page 7, lines 15-19) and the figure legend (page 29, lines 27-29).

We believe these updates improve the clarity and accessibility of our figures and hope they address the reviewer’s concerns.

- note- figure 2 F-G, is semi quantitative, why did the authors not just measure Golgi angle using the nucleus and Golgi distribution?

We appreciate the reviewer’s comment on this point. Following the recommendation, we have performed an additional analysis measuring Golgi orientation angles based on the nucleus-Golgi distribution. This quantitative approach complements our initial semi-quantitative analysis and provides a more precise assessment of Golgi orientation during cell migration.

The new data have been incorporated into Supplementary Figure 1F-H. These results clearly demonstrate the consistency between the quantitative and semi-quantitative methods, further validating our findings and highlighting the dynamic changes in Golgi orientation during cell migration. These changes are described in the Results section (page 6, lines 24-31).

- While it is established that the Golgi is dispersed during reorientation in wound edge migration, the Golgi apparatus also becomes dispersed/less condensed prior to cell division. As the authors have used fixed images - how are they sure that the Golgi morphology or CAMSAP2 localization in 'blue cells' are indicative of Golgi reorientation and not division? Live imaging of cells expressing CAMSAP2, and an additional Golgi marker could be used to demonstrate that the described changes in Golgi morphology and CAMSAP2 localization are occurring during the rear-to-front transition of the Golgi.

Thank you for raising this important question. To address this concern, we carefully examined the nuclear morphology of dispersed Golgi cells and found no evidence of mitotic features, indicating that these cells are not undergoing division (Figure 1A, Supplemental Figure 2A). Furthermore, during the scratch wound assay, we use 2% serum to culture the cells, which helps minimize the impact of cell division. This analysis has been added to the Results section (page7, lines 19-22 in the revised manuscript).

Additionally, we conducted live-cell imaging, as suggested, using cells expressing a Golgi marker. This approach confirmed that Golgi dispersion occurs transiently during reorientation in cell migration. The new live-cell imaging data have been incorporated into Supplementary Figure 2A, and the corresponding description has been updated in the Results section (page 7, lines 2-5).

Finally, considering that overexpression of CAMSAP2 can lead to artifactually condensed Golgi structures, we used endogenous staining to observe CAMSAP2 localization at different stages of migration. These observations provide a clearer understanding of CAMSAP2 dynamics during Golgi reorientation and are now presented in revised Figure 1A-B. This information has been described in the Results section (page 7, lines 5-10).

We hope these additions and clarifications address the reviewer’s concerns. Once again, we are deeply grateful for this constructive feedback, which has greatly improved the robustness of our study.

(2) MARK2 localization to the Golgi apparatus

- The authors investigated the positioning of endogenous MARK2 via immunofluorescence staining, and exogenous flag-tagged MARK2 in a KO background. The description of the protocol required to visualize Golgi localization of MARK2 is inconsistent between the results and methods text. The results text reads as through the 2% serum incubation occurs as a blocking step following fixation. Conversely, the methods section describes the 2% serum incubation as occurring just prior to fixation as a form of serum starvation. The authors need to clarify which of these protocols is correct. Further, whilst I can appreciate that the mechanistic understanding of why serum starvation is required for MARK2 Golgi localization is beyond the scope of the current work, the authors should at a minimum speculate in the discussion as to why they think it might occur.

We sincerely thank the reviewer for the constructive feedback on the localization of MARK2 at the Golgi. Due to the complexity and variability of this phenomenon, we decided to remove the related data from the current manuscript to maintain the rigor of our study. However, we have included a discussion of this phenomenon in the Discussion section (page 13, lines 31-39 and page 14, 1-6in the revised manuscript) and plan to further investigate it in future studies.

The localization of MARK2 at the Golgi was initially observed in experiments following serum starvation, where cells were fixed and stained (The data is not displayed). This observation was supported by the loss of Golgi localization in MARK2 knockdown cells, indicating the specificity of the antibody (The data is not displayed). However, this phenomenon was not consistently observed across all cells, likely due to its transient nature.We speculate that the localization of MARK2 to the Golgi depends on its activity and post-translational modifications. For example, phosphorylation at T595 has been reported to regulate the translocation of MARK2 from the plasma membrane to the cytoplasm (Hurov et al., 2004). Serum starvation might induce modifications or conformational changes in MARK2, leading to its temporary Golgi localization. Additionally, we hypothesize that this localization may coincide with specific Golgi dynamics, such as the transition from dispersed to ribbon-like structures during cell migration.

We also acknowledge the inconsistency in the Results and Methods sections regarding serum starvation. We confirm that serum starvation was performed prior to fixation as an experimental condition, rather than as a blocking step in immunostaining. This clarification has been incorporated into the revised Methods section (page 24, lines 11-12).

We hope this clarification, along with our planned future studies, adequately addresses the reviewer’s concerns. Once again, we deeply appreciate the reviewer’s valuable comments, which have provided important insights for our ongoing work. References：

Hurov, J.B., Watkins, J.L., and Piwnica-Worms, H. (2004). Atypical PKC phosphorylates PAR-1 kinases to regulate localization and activity. Curr Biol 14 (8): 736-741.

- The authors should strengthen their findings by using validated tools/methods consistent with previous publications. i.e. Waterman lab has published two MARK2 constructs- Apple and eGFP tagged versions (doi.org/10.1016/j.cub.2022.04.088), and the localization of MARK2 in U2Os cells (using the same antibody (Anti- MARK2 C-terminal, ABCAM Cat# ab136872). The authors should (1) image the cells live using eGFP-tagged MARK2 during serum starvation to show the dynamics of this localization, (2) image U2Os cells using the abcam ab136872 antibody +/- 2% serum starve. Two MARK2 antibodies are listed in Table 2. Does abcam (ab133724) show a similar localisation?

- The Golgi localization of MARK2 occurs in the absence of the T structural domain, but not when full length MARK2 is expressed. The authors conclude the T- domain is likely inhibitory. When combined with the requirement for serum starvation for this interaction to occur, the authors should clarify the physiological relevance of these observations.

We sincerely thank the reviewer for their valuable suggestions regarding the use of tools and methods and the physiological relevance of MARK2 localization to the Golgi. Regarding the question of how MARK2 itself localizes to the Golgi, we are currently unable to fully elucidate the underlying mechanism. Therefore, we have removed the discussion of MARK2’s Golgi localization from the manuscript to ensure scientific accuracy. However, Below, we provide our detailed response as soon as possible:

First, regarding the suggestion to use tools and methods developed by the Waterman lab to strengthen our findings, we have carefully evaluated their applicability. In our live-cell imaging experiments, we found that full-length MARK2 does not stably localize to the Golgi, even under serum starvation conditions. However, truncated MARK2 mutants lacking the Tail (T) domain exhibit robust Golgi localization. Furthermore, our immunofluorescence staining results indicate that the Spacer domain is the minimal region required for MARK2 localization at the Golgi. Based on these findings, we believe that live-cell imaging of EGFP-tagged full-length MARK2 may not effectively reveal the dynamics of its Golgi localization. However, we plan to focus on the truncated constructs in future studies to better explore the mechanisms underlying MARK2's dynamic behavior. 

Regarding the use of the ab136872 antibody to stain U2OS cells with and without serum starvation, we note that the protocol described by the Waterman lab involves pre-fixation and permeabilization steps, which are not compatible with live-cell imaging. Additionally, we observed that MARK2 Golgi localization appears to be condition-dependent and may coincide with specific Golgi dynamics, such as transitions from dispersed stacks to intact ribbon structures. These events are likely brief and challenging to capture consistently. Nevertheless, we recognize the value of this experimental design and plan to adapt the staining conditions in future work to validate our results further. As for the ab133724 antibody listed in Table 2, we clarify that it has only been validated for Western blotting in our study and does not yield reliable results in immunofluorescence experiments. For this reason, all immunofluorescence staining in this study relied exclusively on ab136872. This distinction has been clarified in the revised Table 2 .

Regarding the hypothesis that the Tail domain of MARK2 is inhibitory, our observations showed that truncated MARK2 mutants lacking the T domain stably localized to the Golgi, whereas fulllength MARK2 did not. Literature evidence supports this hypothesis, as studies on the yeast homolog Kin2 indicate that the C-terminal region (including the Tail domain) binds to the Nterminal catalytic domain to inhibit kinase activity (Elbert et al., 2005). We speculate that serum starvation disrupts this intramolecular interaction, relieving the inhibition by the T domain, activating MARK2, and promoting its localization to the Golgi. Moreover, we hypothesize that the transient nature of MARK2 localization to the Golgi may be related to specific Golgi remodeling processes, such as the transition from dispersed stacks to intact ribbon structures during cell migration or polarity establishment. 

References：

Elbert, M., Rossi, G., and Brennwald, P. (2005). The yeast par-1 homologs kin1 and kin2 show genetic and physical interactions with components of the exocytic machinery. Mol Biol Cell 16 (2): 532-549.

(3) Phosphorylation of CAMSAP2 by MARK2

- The authors examined the effects of MARK2 phosphorylation of CAMSAP2 on Golgi architecture through expression of WT-CAMSAP2 and two CAMSAP2 S835 mutants in CAMSAP2 KO cells. They find that CAMSAP2 S835A (non-phosphorylatable) was less capable of rescuing Golgi morphology than CAMSAP2 S835D (phosphomimetic). Golgi area has been measured to demonstrate this phenomenon. Representative immunofluorescence images in Fig. 4D appear to indicate that this is the case. However, quantification in Fig. 4E does not show significance between HA-CAMSAP2 and HA-CAMSAP2A that would support the initial claim. The authors could analyze other aspects of Golgi morphology (e.g. number of Golgi fragments, degree of dispersal around the nucleus) to capture the clear structural defects demonstrated in HACAMSAP2A cells.

We sincerely thank the reviewer for their valuable feedback and for pointing out potential areas of improvement in our analysis of Golgi morphology. We apologize for any misunderstanding caused by our description of the results in Figure 4E.

The quantification indeed shows a significant difference between HA-CAMSAP2 and HACAMSAP2A in terms of Golgi area, as indicated in the figure by the statistical annotations (pvalue provided in the legend). To ensure clarity, we have revised the figure legend (page 32, lines 19-23 in the revised manuscript) to explicitly describe the statistical significance, and the method used for quantification.

Because the quantification indeed shows a significant difference between HA-CAMSAP2 and HA-CAMSAP2A in terms of Golgi area, and to maintain consistency throughout the manuscript, we did not further analyze other aspects of Golgi morphology.

We hope this clarification, along with the additional analyses, will address the reviewer’s concerns. Once again, we are deeply grateful for these constructive comments, which have helped us improve the quality and robustness of our study.

- Wound edge assays are used to capture the difference in Golgi reorientation towards the leading edge between CAMSAP2 S835A and CAMSAP2 S835D. However, these studies lack comparison to WT-CAMSAP2 that would support the role of phosphorylated CAMSAP2 in reorienting the Golgi in this context.

We sincerely thank the reviewer for their insightful suggestion. In response, we have added a comparison between CAMSAP2 S835A/D and WT-CAMSAP2, in addition to HT1080 and MARK2 KO cells, to better evaluate the role of phosphorylated CAMSAP2 in Golgi reorientation.

The results, now shown in Figure 5A-C, indicate that in the absence of MARK2, there is no significant difference in Golgi reorientation between WT-CAMSAP2 and CAMSAP2 S835A. This observation supports the conclusion that MARK2-mediated phosphorylation of CAMSAP2 at S835 is essential for effective Golgi reorientation.

To enhance clarity, we have updated the corresponding Results section (page 9, lines 37-40 and page 10, line 1 in the revised manuscript) to describe this additional comparison. We believe this analysis strengthens our findings and provides a clearer understanding of the role of phosphorylated CAMSAP2 in Golgi dynamics.

We hope this additional data addresses the reviewer’s concerns. Once again, we are grateful for the constructive feedback, which has helped improve the clarity and robustness of our study.

(4) Identification of CAMSAP2 interaction partners

- Quantification of interaction ability between CAMSAP2 and CG-NAP, CLASP2, or USO1 in Fig. 5D, 5F and 5J respectively, lack WT-CAMSAP2 comparisons.

We sincerely thank the reviewer for their valuable suggestion. In response, we have included WT-CAMSAP2 data in the quantification of interaction ability between CAMSAP2 and CG-NAP, CLASP2, and USO1. These results, now shown in revised Figures 5 D-G and Figures 6 C-D, provide a direct comparison that further validates the differential interaction abilities of CAMSAP2 mutants.

The inclusion of WT-CAMSAP2 allows us to better contextualize the effects of specific mutations on CAMSAP2 interactions and strengthens our conclusions regarding the role of these interactions in Golgi dynamics.

We hope this addition addresses the reviewer’s concerns and enhances the clarity and robustness of our study. We deeply appreciate the constructive feedback, which has been instrumental in improving our manuscript.

- The CG-NAP immunoblot presented in Fig. 5C shows that the protein is 310 kDa, which is the incorrect molecular weight. CG-NAP (AKAP450) should appear at around 450 kDa. Further, no CG-NAP antibody is included in Table 2 - Information of Antibodies. The authors need to explain this discrepancy.

We sincerely apologize for the lack of clarity in our annotation and description, which may have caused confusion regarding the CG-NAP immunoblot presented in Figure 5C (Figure 5D in the revised manuscript). To clarify, CG-NAP (AKAP450) is indeed a 450 kDa protein, and the marker at 310 kDa represents the molecular weight marker’s upper limit, above which CG-NAP is observed. This has been clarified in the figure legend (page 33, lines 21-23 in the revised manuscript).

Regarding the CG-NAP antibody, it was custom-made and purified in our laboratory. Polyclonal antisera against CG-NAP, designated as αEE, were generated by immunizing rabbits with GSTfused fragments of CG-NAP (aa 423–542). This antibody has been validated extensively in our previous research, demonstrating its specificity and reliability (Wang et al., 2017). The details of the antibody preparation are included in the footnote of Table 2 for reference.

We hope this clarification, along with the additional context regarding the antibody validation, resolves the reviewer’s concerns. We are deeply grateful for the reviewer’s attention to detail, which has helped us improve the clarity and rigor of our manuscript.

References：

Wang, J., Xu, H., Jiang, Y., Takahashi, M., Takeichi, M., and Meng, W. (2017). CAMSAP3dependent microtubule dynamics regulates Golgi assembly in epithelial cells. Journal of genetics and genomics = Yi chuan xue bao 44 (1): 39-49.

Minor Comments

- Authors should change immunofluorescence images to colorblind friendly colors. The current presentation of merged overlays makes it really difficult to interpret- I would strongly encourage inverted or at a minimum greyscale individual images of key proteins of interest.

We sincerely thank the reviewer for their valuable suggestion regarding the presentation of immunofluorescence images. In response, we have converted the images in Figure 1C to greyscale individual images for each key protein of interest. This adjustment ensures that the figures are more accessible and interpretable, including for readers with color vision deficiencies.

We hope this modification addresses the reviewer’s concern and improves the clarity of our data presentation. We are grateful for the constructive feedback, which has helped us enhance the overall quality of our figures.

- On p. 8 text should be amended to 'Previous literature has documented MARK2's localization to the microtubules, microtubule-organizing center (MTOC), focal adhesions..'

We sincerely thank the reviewer for their comment regarding the text on page 8. Considering the reasoning provided in response to question 2, where we clarified that MARK2's Golgi localization is not fully understood, we have decided to remove this section from the manuscript to maintain the accuracy and rigor of our study.

We appreciate the reviewer’s attention to detail and constructive feedback, which has helped us improve the clarity and focus of our manuscript. 

- In Fig.1A scale bars are not shown on individual channel images of CAMSAP or GM130

We sincerely thank the reviewer for pointing out the omission of scale bars in the individual channel images of CAMSAP and GM130 in Figure 1A (Figure 1C in the revised manuscript). In response, we have added a scale bar (5 μm) to the CAMSAP2 channel, as shown in the revised Figure 1C. These updates have been described in the figure legend (page 29, line 21).

We hope this modification addresses the reviewer’s concern and improves the accuracy and clarity of our figure presentation. We greatly appreciate the reviewer’s constructive feedback, which has helped enhance the quality of our manuscript.

- In Fig. 1B the title should be amended to 'Colocalization of CAMSAP2/GM130'

We sincerely thank the reviewer for their suggestion to amend the title in Figure 1B (Figure 1D in the revised manuscript). In response, we have updated the title to "Colocalization of CAMSAP2/GM130," as shown in the revised Figure 1D.

We hope this modification addresses the reviewer’s concern and improves the clarity and accuracy of the figure. We greatly appreciate the reviewer’s valuable feedback, which has helped us refine the presentation of our results.

- In Fig. 2F, 5A, and Sup Fig 3C scale bars have been presented vertically

We sincerely thank the reviewer for pointing out the issue with the vertical orientation of scale bars in Figures 2F (Figure 2D in the revised manuscript), 5A, and Supplementary Figure 3C. In response, we have modified the scale bars in revised Figures 2D and 5A to a horizontal orientation for improved consistency and clarity. Additionally, Supplementary Figure 3C has been removed from the revised manuscript.

We hope these adjustments address the reviewer’s concerns and enhance the overall presentation quality of the figures. We greatly appreciate the reviewer’s constructive feedback, which has helped us refine our manuscript.

- Panels are not correctly aligned, and images are not evenly spaced or sized in multiple figures - Fig. 2F, 4D, Sup Fig. 1F, Sup Fig. 2C, Sup Fig. 3E, Sup Fig. 4C

We sincerely thank the reviewer for pointing out the misalignment and uneven spacing or sizing of panels in multiple figures, including Figures 2F, 4D, Supplementary Figures 1F, 2C, 3E, and 4C (Figure 2D, 4D, Supplementary Figures 1F, 2C, and 3H in the revised manuscript.

Supplementary Figure 3E was removed from our manuscript). In response, we have standardized the spacing and sizing of all panels throughout the manuscript to ensure consistency and improve visual clarity.

We hope this modification addresses the reviewer’s concerns and enhances the overall presentation quality of our figures. We greatly appreciate the reviewer’s constructive feedback, which has helped us improve the organization and professionalism of our manuscript.

- An uncolored additional data point is present in Fig. 3F

We sincerely thank the reviewer for pointing out the presence of an uncolored additional data point in Figure 3F. In response, we have removed this data point from the revised figure to ensure accuracy and clarity.

We hope this adjustment resolves the reviewer’s concern and improves the overall quality of the figure. We greatly appreciate the reviewer’s careful review and constructive feedback, which have helped us refine our manuscript.

- In Fig. 3A 'GAMSAP2/GM130' in the vertical axis label should be amended to 'CAMSAP2/GM130'

We sincerely thank the reviewer for pointing out the error in the vertical axis label of Figure 3A. In response, we have corrected "GAMSAP2/GM130" to "CAMSAP2/GM130," as shown in the revised Figure 3I.

We hope this correction resolves the reviewer’s concern and improves the accuracy of our figure. We greatly appreciate the reviewer’s careful review and constructive feedback, which have helped us refine our manuscript.

- In Fig 5A the green label should be amended to 'GFP-CAMSAP2' instead of 'GFP'

We sincerely apologize for the confusion caused by our labeling in Figure 5A. To clarify, the green label “GFP” refers to the antibody used, while “GFP-CAMSAP2” is indicated at the top of the figure to specify the construct being analyzed.

We hope this explanation resolves the misunderstanding and provides clarity regarding the labeling in Figure 5A. We greatly appreciate the reviewer’s feedback, which has allowed us to address this issue and improve the precision of our figure annotations.

- The repeated use of contractions throughout the manuscript was distracting, I would strongly encourage removing these.

We sincerely thank the reviewer for pointing out the distracting use of contractions in the manuscript. In response, we have removed and replaced all contractions with their full forms to improve the clarity and formal tone of the text.

We hope this modification addresses the reviewer’s concern and enhances the readability and professionalism of our manuscript. We greatly appreciate the reviewer’s constructive feedback, which has helped us refine the quality of our writing.

Reviewer #2: 

Summary  

This work by the Meng lab investigates the role of the proteins MARK2 and CAMSAP2 in the Golgi reorientation during cell polarisation and migration. They identified that both proteins interact together and that MARK2 phosphorylates CAMSAP2 on the residue S835. They show that the phosphorylation affects the localisation of CAMSAP2 at the Golgi apparatus and in turn influences the Golgi structure itself. Using the TurboID experimental approach, the author identified the USO1 protein as a protein that binds differentially to CAMSAP2 when it is itself phosphorylated at residue 835. Dissecting the molecular mechanisms controlling Golgi polarisation during cell migration is a highly complex but fundamental issue in cell biology and the author may have identified one important key step in this process. However, although the authors have made a genuine iconographic effort to help the reader understand their point of view, the data presented in this study appear sometimes fragile, lacking rigour in the analysis or over-interpreted. Additional analyses need to be conducted to strengthen this study and elevate it to the level it deserves.

We sincerely thank the reviewer for their thoughtful evaluation and recognition of our study's significance in understanding Golgi reorientation during cell migration. We appreciate the constructive feedback regarding data robustness, clarity, and interpretation. In response, we have conducted additional analyses, revised data presentation, and ensured cautious interpretation throughout the manuscript. These changes aim to address the reviewer’s concerns comprehensively and strengthen the scientific rigor of our study.

Major comments

In order to conclude as they do about the putative role of USO1, the authors need to perform a siRNA/CRISPR of USO1 to validate its role in anchoring CAMSAP2 to the Golgi apparatus in a MARK2 phosphorylation-dependent manner. In other words, does depletion of USO1 affect the recruitment of CAMSAP2 to the Golgi apparatus?

We sincerely thank the reviewer for their insightful suggestion regarding the role of USO1 in anchoring CAMSAP2 to the Golgi apparatus. In response, we performed USO1 knockdown using siRNA and quantified the Pearson correlation coefficient of CAMSAP2 and GM130 colocalization in control and USO1-knockdown cells.

The results show that CAMSAP2 localization to the Golgi is significantly reduced in USO1knockdown cells, confirming that USO1 plays a critical role in recruiting CAMSAP2 to the Golgi apparatus. These results are now presented in Figures 6 E–G, and corresponding updates have been incorporated into the Results section (page 10, lines 36-37 in the revised manuscript).

We hope this additional experiment addresses the reviewer’s concern and strengthens our conclusions regarding the role of USO1. We are grateful for the reviewer’s constructive feedback, which has greatly improved the robustness of our study.  

It is not clear from this study exactly when and where MARK2 phosphorylates CAMSAP2. What is the result of overexpression of the two proteins in their respective localisation to the Golgi apparatus? As binding between CAMSAP2 and MARK2 appears robust in the immunoprecipitation assay, this should be readily investigated. 

We sincerely thank the reviewer for their insightful comments and questions. To address the role of MARK2 in regulating CAMSAP2 localization to the Golgi apparatus, we overexpressed GFPMARK2 in cells and compared its effects on CAMSAP2 localization to the Golgi with control cells overexpressing GFP alone. Our results show that CAMSAP2 localization to the Golgi is significantly increased in GFP-MARK2-overexpressing cells, as shown in Supplementary Figures 3C and 3E. Corresponding updates have been incorporated into the Results section (page 8, lines 25-27 in the revised manuscript).

Regarding the question of how MARK2 itself localizes to the Golgi, we are currently unable to fully elucidate the underlying mechanism. Therefore, we have removed the discussion of MARK2’s Golgi localization from the manuscript to ensure scientific accuracy. Consequently, we have not conducted experiments to assess the effects of CAMSAP2 overexpression on MARK2’s localization to the Golgi.

We hope this explanation clarifies the reviewer’s concerns. We are grateful for the reviewer’s constructive feedback, which has guided us in improving the clarity and focus of our study.

To strengthen their results, can the author map the interaction domains between CAMSAP2 and MARK2? The authors have at their disposal all the constructs necessary for this dissection.

We sincerely thank the reviewer for their insightful suggestion to map the interaction domains between CAMSAP2 and MARK2. In response, we performed immunoprecipitation experiments using truncated constructs of CAMSAP2. Our results reveal that MARK2 interacts specifically with the C-terminus (1149F) of CAMSAP2, as shown in Supplementary Figures 3A and 3B. Corresponding updates have been incorporated into the Results section (page 7, lines 41-42 and page 8, line 1 in the revised manuscript).

We hope this additional analysis addresses the reviewer’s suggestion and further strengthens our conclusions. We greatly appreciate the reviewer’s constructive feedback, which has helped improve the depth of our study.

Minor comments

Sup-fig1  

H: It is not clear if the polarisation experiment has been repeated three times (as it should) and pooled or is just the result of one experiment?

We sincerely apologize for the lack of clarity regarding the experimental details for Supplementary Figure 1H. To clarify, the polarization experiment was repeated three times, and the results were pooled to generate the data presented. We have updated the figure legend for Supplementary Figure 1H to explicitly state this information (page 35, lines 27-29 in the revised manuscript).

We hope this clarification resolves the reviewer’s concern. We greatly appreciate the reviewer’s careful review and constructive feedback, which have helped us improve the accuracy and transparency of our manuscript.

Sup-fig2  

C: "Immunofluorescence staining plots" formula used in the legend is not clear. Which condition is presented in the panel, parental HT1080 or CAMSAP2 KO cells?  

We thank the reviewer for pointing out the lack of clarity regarding the conditions presented in Supplementary Figure 2C. To clarify, the immunofluorescence staining plots shown in this panel are from parental HT1080 cells. We have updated the figure legend to include this information (page 36, line 14 in the revised manuscript).

We hope this clarification resolves the reviewer’s concern and improves the transparency of our data presentation. We greatly appreciate the reviewer’s feedback, which has helped us refine the manuscript.

Figure 1  

D: In the plot, the colour of the points for the "red cells" are red but the one for the "blue cells" are green, this is confusing.

E: Once again, the colour choice is confusing as blue cells (t=0.5h) are quantified using red dots and red cells (t=2h) quantified using green dots. The t=0h condition should be quantified as well and added to the graph.  

F: Representative CAMSAP2 immunofluorescence pictures for the three time points should be provided in addition to the drawings.  

We thank the reviewer for their valuable comments regarding Figure 1D (revised Figure 1E), Figure 1E (revised Figure 1B), and Figure 1F (revised Supplementary Figure 2C).

- Figure 1D (revised Figure 1E): we have modified the x-axis labels and adjusted the color scheme of the data points to ensure consistency and avoid confusion.

- Figure 1E (revised Figure 1B): we have updated the x-axis and included the quantification of the t=0h condition, which has been added to the graph.

- Figure 1F (revised Supplementary Figure 2C): we have provided representative immunofluorescence images of CAMSAP2 for the three-time points to complement the schematic drawings.

We hope these revisions address the reviewer’s concerns and improve the clarity and completeness of our data presentation. We greatly appreciate the reviewer’s constructive feedback, which has significantly contributed to enhancing our manuscript.

Figure 2  

A: No methodology in the material and methods is provided for this analysis.  

B: Can the authors be more precise regarding the source of the CAMSAP2 interactants? Can the author provide the citation of the publication describing the CAMSAP2-MARK2 interaction?  

D: Genotyping for the MARK2 KO cell line should be provided the same way it was provided for the CAMSAP2 cell line in Sup-fig1. "MARK2 was enriched around the Golgi apparatus in a  significant proportion of HT1080 cells": which proportion of the cells?  

F: The time point of fixation is missing  

G: It is not clear if the polarisation experiment has been repeated three times (as it should) and pooled or is just the result of one experiment?  

We thank the reviewer for their detailed comments and suggestions regarding Figure 2. Below, we provide clarifications and outline the modifications made:

- Figure 2A: The methodology for this analysis has been added to section 5.14 (Data statistics). Specifically, we have stated: “GO analysis of proteins was plotted using https://www.bioinformatics.com.cn, an online platform for data analysis and visualization” (page 26 lines 5-6 in the revised manuscript).

- Figure 2B: The CAMSAP2 interactants were derived from the study by Wu et al., 2016, which provides the source of these interactants. The interaction between CAMSAP2 and MARK2 is referenced from Zhou et al., 2020. These citations have been added to the relevant sections of the manuscript (page 30, lines 10-11 and 13-14).

- Figure 2D (removed in the revised manuscript): Genotyping for the MARK2 KO cell line has been provided in the same format as for the CAMSAP2 KO cell line in Figure 2G. Additionally, as the MARK2 Golgi localization discussion cannot yet be fully elucidated, we have removed this portion from the manuscript.

- Figure 2F (revised Figure 2D): The time point of fixation, which occurred 2 hours after the scratch wound assay, has been added to the figure legend (page 30, lines 15-16).

- Figure 2G (revised Figure 2E-F): The polarization experiment was repeated three times, and the results were pooled. This information has been included in the figure legend (page 30, lines 26 and 29).

We hope these updates address the reviewer’s concerns and improve the clarity and completeness of the manuscript. We are grateful for the reviewer’s constructive feedback, which has greatly enhanced the rigor of our study. References：

Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.

Sup-fig3  

E: Although colocalisation between CAMSAP2 and MARK2 is clear in your serum conditions in HT1080 and RPE1 cells, the deletion domain analysis appears weak and insufficient to implicate the role of the spacer domain. This part should be deleted or strengthened, but the data do not satisfactorily support your conclusion as it stands.  

We sincerely thank the reviewer for their critical comments regarding the deletion domain analysis of MARK2 and its role in colocalization with CAMSAP2. As the current data do not satisfactorily support our conclusions, we have removed all related content on MARK2 and the deletion domain analysis from the manuscript to maintain scientific rigor.

We appreciate the reviewer’s valuable feedback, which has helped us refine and improve the quality and focus of our study.

Figure 3  

A: Can the reduced CAMSAP2 Golgi localisation phenotype be rescued by the overexpression of MARK2 cDNA in the MARK2 KO cells?  

F: Presence of a white dot on the HT1080 plot  

G: The composition of the homogenization buffer is not indicated in the material and methods  

We thank the reviewer for their valuable comments and suggestions regarding Figure 3. Below, we detail the modifications made:

- Figure 3A: To address whether the reduced CAMSAP2 Golgi localization phenotype can be rescued, we overexpressed MARK2 cDNA in MARK2 KO cells. Our results show that overexpression of MARK2 successfully rescues the reduced CAMSAP2 localization to the Golgi, as demonstrated in Supplementary Figures 3C and 3E (page 8, lines 5-7).

- Figure 3F: We have removed the white dot on the HT1080 plot to ensure clarity and accuracy.

- Figure 3G: The composition of the homogenization buffer used in the experiment has been added to the Materials and Methods section for completeness (page 24, lines 34-41 and page 25, lines 1-10).

We hope these revisions address the reviewer’s concerns and enhance the clarity and rigor of our study. We are grateful for the reviewer’s constructive feedback, which has significantly improved the quality of our manuscript.

Figure 4  

B: Quantification of the effect of the S835A mutation should be provided  

D: Top left panel: Why Ha antibody stains Golgi structure in absence of Ha-CAMSAP2 transfection ? IF the Ha antibody has unspecific affinity towards the Golgi apparatus, may be it is not the good tag to use in this assay?  

E: The number of cells studied should be standardized. 119 cells were analyzed in the CAMSAP KO vs only 35 cells in the CAMSAP2 KO (HA-CAMSAP2-S835D) conditions. This could introduce strong bias to the analysis. Furthermore the CAMSAP2 S835A seems to provide a certain level of rescue. It would be interesting to see what is the result of the T test between the HT1080 and HA-CAMSAP S835A conditions.  

We thank the reviewer for their thoughtful comments and suggestions regarding Figure 4. Below, we detail the revisions and clarifications made:

- Figure 4B: The S835A mutation renders CAMSAP2 non-phosphorylatable by MARK2. This conclusion is based on our experimental observations and previously reported mechanisms.

- Figure 4D: The HA antibody does not exhibit non-specific affinity toward the Golgi apparatus. The observed labeling in the top left panel was due to an error in our annotation. We have corrected the label, replacing "HA" with "CAMSAP2" to accurately reflect the experimental conditions.

- Figure 4E: To standardize the number of cells analyzed across conditions, we reduced the number of CAMSAP2 KO cells analyzed to 50 and balanced the sample sizes for comparison. Additionally, we performed a t-test between the HT1080 and HACAMSAP2 S835A conditions. The results support that CAMSAP2 S835A provides partial rescue, as reflected in the updated analysis (page 32, lines 19-23).

We hope these revisions address the reviewer’s concerns and improve the accuracy and reliability of our results. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the quality of our study.

Figure 6  

6A: The wound position should be indicated on the picture.  

6B: Given that microtubule labelling is present on the vast majority of the cell surface, this type of quantification provides very little information using conventional light microscopy and should not be used to conclude any change in the microtubule network using Pearson's coefficient.  The text describing the figure 6A and 6B needs re written as I do not understand what the author want to say. "In cells located before the wound edge..." : I do not understand how a cell could be located before the wound edge. Which figure corresponds to the trailing edge of the wounding?

We thank the reviewer for their valuable comments on Figure 6A (revised Supplementary Figure 6E) and Figure 6B (revised Supplementary Figure 6F). Below, we detail the modifications made:

- Figure 6A (revised Supplementary Figure 6E), we have added arrows to indicate the wound position, providing clearer guidance for interpreting the image.

- Figure 6B (revised Supplementary Figure 6F), we revised our quantification method based on the approach used in literature (Wu et al., 2016). Specifically, we analyzed the relationship between microtubules and the Golgi apparatus in cells at the leading edge of the wound. The x-axis represents the distance from the Golgi center, while the y-axis shows the normalized radial fluorescence intensity of microtubules and the Golgi apparatus.

Additionally, we revised the accompanying text for clarity and accuracy. The original description:

“In cells located before the wound edge, the Golgi apparatus maintained a ribbon-like shape, with a higher density of microtubules. In contrast, at the trailing edge of the wounding, the Golgi apparatus appeared more as stacks around the nucleus, with fewer microtubules”  was replaced with:

“Finally, to comprehensively understand the dynamics between non-centrosomal microtubules and the Golgi apparatus during Golgi reorientation, we conducted cell wound-healing experiments (Supplementary Figure 6 E-F). Our observations revealed notable changes in the Golgi apparatus and microtubule network distribution in relation to the wounding. These findings corroborate our earlier results and suggest a highly dynamic interaction between the Golgi apparatus and microtubules during Golgi reorientation” (Revised manuscript page 11 lines 3-10).

We hope these changes address the reviewer’s concerns and improve the clarity and robustness of our study. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the presentation and interpretation of our data. References：

Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.

Reviewer #3:  

Summary  

In this study, Xu et al. analyzed the wound healing process of HT1080 cells to elucidate the molecular mechanisms by which the Golgi apparatus exhibits transient dispersion before reorienting to the wound edge in the compact assembly structure. They focused on the role of the microtubule minus-end binding protein CAMSAP2, which mediates the linkage between microtubules and the Golgi membrane. At first, they noticed that CAMSAP2 transiently lost Golgi colocalization during the initial phase of the wound healing process. They further found that the cell polarity-regulating kinase MARK2 binds and phosphorylates S835 of CAMSAP2, thereby enhancing the interaction between CAMSAP2 and the Golgi protein Uso1. Together with the phenotypes of CAMSAP2, MARK2, and Uso1 KO cells, these authors argue that the MARK2dependent phosphorylation of CAMSAP2 plays an important role in the reassembly and reorientation of the Golgi apparatus after a transient dispersion observed during the wound healing process.

We sincerely thank the reviewer for their thoughtful summary of our study and constructive feedback. Your comments have been invaluable in refining our research and enhancing the clarity and impact of our manuscript.

Major comments

(1) The premise of this study was that during the wound healing process, the Golgi apparatus exhibits transient dispersion before reorientation to the front of the nucleus.  

In the first place, this claim has not been well established in previous studies or this paper. Therefore, the authors should present a proof of this claim in a clearer manner.  

To introduce this cellular event, the authors cite several papers in the introduction (page 4) and the results (page 6) sections. However, many papers cited are review articles, and some of them do not describe this change in the Golgi assembly structure before reorientation. Only two original articles discussed this phenomenon (Bisel et al. 2008 and Wu et al. 2016), and direct evidence was provided by only one paper (Wu et al. 2016) in which changes in the Golgi apparatus in wound-healing RPE1 cells were recorded by live imaging (Fig.7A in Wu et al. 2016).

Furthermore, it should be noted that this previous paper demonstrated that depletion of CAMSAP2 inhibits Golgi dispersion. Obviously, this conclusion is inconsistent with their statement to introduce this study (page4) that ‟This emphasizes CAMSAP2's role in sustaining Golgi integrity during critical cellular events like migration." In addition, it also contradicts the authors' model of the present paper (Fig. 6E), which argued that disruption of the Golgi association of CAMSAP2 facilitates the Golgi dispersion.  

We sincerely thank the reviewer for their detailed comments and for providing us with the opportunity to clarify the premise and conclusions of our study. Below, we address the main concerns raised:

First, to provide direct evidence of Golgi apparatus changes during the wound-healing process, we conducted live-cell imaging experiments. Our observations, presented in revised Supplementary Figure 2A, clearly demonstrate that the Golgi apparatus exhibits a transient dispersion state before reorienting toward the leading edge of the nucleus during migration.

Regarding the interpretation of previous studies, we acknowledge the reviewer’s concerns about the citation of review articles. To address this, we have revisited the literature and clarified that the phenomenon of Golgi dispersion during reorientation has been directly demonstrated in Wu et al (Wu et al., 2016), where live imaging of wound-healing RPE1 cells showed this dynamic behavior. Furthermore, we note that in Wu et al paper explicitly demonstrates that CAMSAP2 depletion promotes Golgi dispersion, contrary to the reviewer’s interpretation that "depletion of CAMSAP2 inhibits Golgi dispersion."

Our model focuses on the role of CAMSAP2 in restoring the Golgi from a transiently dispersed structure back to an intact ribbon-like structure during reorientation. Specifically, we propose that during this process, the disruption of CAMSAP2’s association with the Golgi affects this restoration, rather than directly promoting Golgi dispersion as suggested by the reviewer. We believe this distinction aligns with our data and the existing literature.

To strengthen the background of our study, we have revised the introduction and results sections (page 6, lines 6-13 and page 7, lines 1-17) to minimize reliance on review articles and have provided more explicit citations to original research papers. We hope this addresses the reviewer’s concern about the sufficiency of the cited literature.

We trust these clarifications and revisions resolve the reviewer’s concerns and enhance the robustness of our study. Once again, we are grateful for the reviewer’s constructive feedback, which has greatly helped refine our manuscript. References：

Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.

The authors did not provide experimental data for this temporal change in the Golgi assembly structures during the wound-healing process of HT1080 that they analyzed. They only provide an illustration of wound-healing cells (Fig.1F), in which cells are qualitatively discriminated and colored based on the Golgi states, without indicating the experimental basis of the discrimination.

According to their ambiguous descriptions in the text (page7), the reader can speculate that Fig. 1F is illustrated based on the images in Supplementary Fig. 2C. However, because of the low quality and presentation style of these data, it is impossible to recognize the assembly structures of the Golgi apparatus in wound-edge cells.  

If the authors hope to establish this premise claim for the present paper, they should provide their own data corresponding to the present Supplementary Fig. 2C in more clarity and present qualitative data verifying this claim, as Wu et al. did in Fig. 7A in their paper.

We sincerely thank the reviewer for their constructive feedback and the opportunity to address the concern regarding the lack of experimental data supporting the temporal changes in Golgi assembly during the wound-healing process.

To establish this premise, we conducted live-cell imaging experiments to observe the dynamic changes in the Golgi apparatus during directed cell migration. Our data, now presented in Supplementary Figure 2A, clearly demonstrate that the Golgi apparatus undergoes a transient dispersed state before reorganizing into an intact structure. These findings provide direct experimental evidence supporting our claim.

In addition, we have revised the data originally presented in Supplementary Figure 2C and enhanced its quality and presentation style. This supplementary figure now includes clearer images and annotations to better illustrate the Golgi assembly structures in wound-edge cells. The improved data presentation aligns with the standards set by Wu et al reported (Wu et al., 2016) and provides qualitative support for our observations.

We hope these additions and revisions address the reviewer’s concerns and strengthen the scientific rigor and clarity of our manuscript. We are grateful for the reviewer’s valuable suggestions, which have significantly improved the quality of our study. References：

Wu, J., de Heus, C., Liu, Q., Bouchet, B.P., Noordstra, I., Jiang, K., Hua, S., Martin, M., Yang, C., Grigoriev, I., et al. (2016). Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Dev Cell 39 (1): 44-60.

(2) In Fig.1A-D, the authors claim that CAMSAP2 dissociates from the Golgi apparatus in cells "that have not yet completed Golgi reorientation and exhibit a transitional Golgi structure, characterized by relative dispersion and loss of polarity (page7)." However, I these analyses, they do not analyze the initial stage (0.5h after wound addition) of cells facing the wound edge, as they do in Supplementary Fig. 2C. Instead, they analyze cells separated from the wound edge at 2 h after wound addition when the wound-edge cells complete their polarization. These data are highly misleading because there is no evidence that the cells separated from the wound edge are really in the transitional state before polarization.  

In this regard, Fig. 1E shows the analysis of the wound-edge cells at 0.5 and 2 h after the addition of wound, which provides suitable data to verify the authors' claim. However, the corresponding legend indicates that these statistical data are based on the illustration in Fig. 1F, which is probably based on highly ambiguous data in Supplementary Fig. 2C (see above).  

Taken together, I strongly recommend the authors to remove Fig.1A-D. Instead, they should include the improved figure corresponding to the present Supplementary Fig.2C and present its statistical analysis similar to the present Fig.1E for this claim.

We sincerely thank the reviewer for their constructive feedback and recommendations. Below, we address the concerns raised regarding Figure 1A-D and Supplementary Figure 2C.

To provide stronger evidence for the transitional state of the Golgi apparatus during reorientation and the dynamic regulation of CAMSAP2 localization, we conducted live-cell imaging experiments. These results, now presented in Supplementary Figure 2A, clearly demonstrate that the Golgi apparatus undergoes a transitional state characterized by dispersion before reorienting toward the leading edge.

Additionally, we analyzed fixed wound-edge cells at different time points during directed migration to observe CAMSAP2’s colocalization with the Golgi apparatus. The results, shown in Figures 1A and 1B, reveal dynamic changes in CAMSAP2 localization, confirm its regulation during Golgi reorientation, and include a corresponding statistical analysis (page 7, lines 1-17).

These updates ensure that our claims are supported by robust and unambiguous data.

We hope these revisions address the reviewer’s concerns and provide clear and reliable evidence for the transitional state of the Golgi apparatus and CAMSAP2’s dynamic regulation. We are grateful for the reviewer’s constructive suggestions, which have greatly improved the quality and focus of our manuscript.

(3) In Supplementary Fig. 5 and Fig. 4, the authors claim that MARK2 phosphorylates S835 of CAMSAP2.  

There are many issues to be addressed. Otherwise, the above claim cannot be assumed to be reliable.  

First, the descriptions (in the text and method sections) and figures (Supplementary Fig.5) concerning the in vitro kinase assay and subsequent phosphoproteomic analysis are too immature and contain many errors.  

Legend to Supplementary Fig. 5 is too immature for comprehension. It should be completely rewritten in a more comprehensive manner. The figure in Supplementary Fig. 5C is also too immature for understanding. They simply paste raw mass spectrometric data without any modification for presentation.  

We sincerely apologize for the lack of clarity and inaccuracies in the original descriptions and figure legends for the in vitro kinase assay and phosphoproteomic analysis. We greatly appreciate the reviewer’s detailed comments, which have allowed us to address these issues comprehensively.

To improve clarity and accuracy, we have rewritten the figure legend for the original Supplementary Figure 5 (now Supplementary Figure 4) as follows:

(A): CBB staining of a gel with GFP-CAMSAP2, GST, and GST-MARK2. GFP-CAMSAP2 was expressed in Sf9 cells and purified. GST and GST-MARK2 were expressed in E. coli and purified.

(B): Western blot analysis of an in vitro kinase assay. GST or GST-MARK2 was incubated with GFP-CAMSAP2 in kinase buffer (50 mM Tris-HCl pH 7.5, 12.5 mM MgCl2, 1 mM DTT, 400 μM ATP) at 30°C for 30 minutes. Reactions were stopped by boiling in the loading buffer.

(C): Detection of phosphorylation at S835 in CAMSAP2 by mass spectrometry. The observed mass increases in b4, b5, b6, b7, b8, b10, b11, and b12 fragments indicate phosphorylation at Ser835.

(D): Kinase assay samples analyzed using Phos-tag SDS-PAGE. HEK293 cells were cotransfected with the indicated plasmids. Band shifts of CAMSAP2 mutants were examined via western blot. Phos-tag was used in SDS-PAGE, and arrowheads indicate the shifted bands caused by phosphorylation.

To address the reviewer’s concern about Supplementary Figure 5C, we have reformatted the mass spectrometry data to improve readability and presentation quality. The revised figure includes clearer annotations and graphical representations of the mass spectrometric evidence for phosphorylation at S835.

We believe these updates enhance the comprehensibility and reliability of our data, providing robust support for our claim that MARK2 phosphorylates CAMSAP2 at S835. We hope these

revisions address the reviewer’s concerns and demonstrate our commitment to improving the quality of our manuscript.

The readers cannot understand how the authors purified GFP-CAMSAP2 for the kinase assay.

The method section incorrectly states that the product was purified using Ni-resin.  

We thank the reviewer for their comment regarding the purification of GFP-CAMSAP2 for the kinase assay. We would like to clarify that GFP-CAMSAP2 carries a His-tag, which allows for purification using Ni-resin, as described in the Methods section (page 23, Lines 32-40). Therefore, the description in the Methods section is correct.

To avoid any potential misunderstanding, we have revised the Methods section to provide more detailed and precise descriptions of the purification process. Specifically, GFP-CAMSAP2 was cloned into the pOCC6_pOEM1-N-HIS6-EGFP vector, which includes a His-tag, and was expressed in Sf9 cells. The His-GFP-CAMSAP2 protein was purified using Ni-resin chromatography. Relevant details have been added to the Methods section (page 21, Lines 34-36:

“CAMSAP2 was cloned into the pOCC6_pOEM1-N-HIS6-EGFP vector expressed in Sf9, purified as His-GFP-CAMSAP2.”; page 23, Lines 32-33: “His-GFP-CAMSAP2 was cotransfected with bacmids into Sf9 cells to generate the passage 1 (P1) virus.”).

We hope these clarifications and revisions address the reviewer’s concern and improve the comprehensibility of our experimental details. We appreciate the reviewer’s feedback, which has helped us refine the manuscript.

In this relation, GST and GST-MARK2 are described as having been purified from Sf9 insect cells in the text section (page9) and legend to Supplementary Fig. 5, but from E. coli in the method section. Which is correct?  

We thank the reviewer for pointing out the inconsistencies in the descriptions regarding the source of GST and GST-MARK2. To clarify, both GST and GST-MARK2 were purified from E. coli, as stated in the Methods section (page 23, Lines 26-31). We have corrected the erroneous descriptions in the main text (page 8, Lines 35-36) and the legend to Supplementary Figure 4 to ensure consistency.

Additionally, we have updated the legend for Supplementary Figure 4A to state the sources of each protein explicitly:

“GFP-CAMSAP2 were expressed in Sf9 cells and purified. GST and GST-MARK2 were expressed in E. coli and purified.” (page 38, Lines 2-3)

These revisions ensure that the experimental details are accurate and consistent across the manuscript, eliminating any potential confusion. We appreciate the reviewer’s careful review and constructive feedback, which have helped us improve the clarity and reliability of our study.

Because the phosphoproteomic data (Supplementary Fig. 5C) are not provided clearly, the experimental data for Fig.4A, in which possible CAMSAP2 phosphorylation sites are illustrated, are completely unknown. For me, it is highly strange that only the serine residues are listed in Fig. 4A.

We sincerely thank the reviewer for raising this important point regarding Figure 4A and the phosphoproteomic data in Supplementary Figure 5C.

- Phosphorylation Sites in Figure 4A

The phosphorylation sites illustrated in Figure 4A are derived from our analysis of the original mass spectrometry data. These sites were included based on their high confidence scores and data reliability. Importantly, only serine residues met the stringent criteria for inclusion, as no threonine or tyrosine residues had sufficient evidence for phosphorylation. To clarify this, we have updated the figure legend for Figure 4A (page 32, Lines3-7).

- Improvements to Supplementary Figure 5C (Supplementary Figure 4D in the revised manuscript)

To enhance transparency and clarity, we have reformatted Supplementary Figure 4D to include clearer annotations. The revised figure highlights the phosphopeptides used to identify the phosphorylation sites and provides a more comprehensive presentation of the mass spectrometry data. To clarify this, we have updated the figure legend for Supplementary Figure 4D (page 38, Lines 11-13).

- Data Availability

We will follow the journal’s guidelines by uploading the raw mass spectrometry data to the required public database upon manuscript acceptance. This ensures that the data are accessible and reproducible in compliance with journal standards.

We hope these clarifications and updates address the reviewer’s concerns and improve the reliability and comprehensibility of our data presentation. We greatly appreciate the reviewer’s constructive feedback, which has helped us enhance the rigor and clarity of our manuscript.

Considering the crude nature of the GST-MARK2 sample used for the in vitro kinase assay (Supplementary Fig. 5A), it is unclear whether MARK2 is responsible for all phosphorylation sites on CAMSAP2 detected in the phosphoproteomic analysis. Furthermore, if GFP-CAMSAP2 was purified from Sf9 insect cells, these sites might have been phosphorylated before incubation for the in vitro kinase assay. The authors should address these issues by including a negative control using the kinase-dead mutant of MARK2 in their in vitro kinase assay.

We sincerely thank the reviewer for raising these important points regarding the potential prephosphorylation of GFP-CAMSAP2 and the role of MARK2 in the phosphorylation sites detected in our analysis.

To address the possibility that GFP-CAMSAP2 may have been pre-phosphorylated during its expression in Sf9 insect cells, we conducted an in vitro comparison. Specifically, we compared the band shifts observed in GST-MARK2 + GFP-CAMSAP2 versus GST + GFP-CAMSAP2 under identical conditions. As shown in Supplementary Figure 4B, the GST-MARK2 + GFP-CAMSAP2 group exhibited a clear upward band shift compared to the GST + GFP-CAMSAP2 group, indicating additional phosphorylation events induced by MARK2.

Regarding the inclusion of a kinase-dead MARK2 mutant as a negative control, we acknowledge this as a valuable suggestion for further confirming the specificity of MARK2 in phosphorylating CAMSAP2. While this experiment is not currently included, we plan to conduct it in our future studies to strengthen our findings.

We hope this clarification and the provided evidence address the reviewer’s concerns. We are grateful for this constructive feedback, which has helped us critically evaluate and refine our experimental approach.

(4) In Supplementary Fig.6A-C and Fig.5A-B, the authors claim that the phosphorylation of CAMSAP2 S835 is required for restoring the reduced reorientation of the Golgi in wound-healing cells and the delay in wound closure observed in MARK2 KO cells.  

If the aforementioned claim is adequately supported by experimental data, it indicates that the defects in Golgi repolarization and wound closure in MARK2 KO cells can be mainly attributed to the reduced phosphorylation of S835 of CAMSAP2 in HT1080. Considering the presence of many well-known substrates of MARK2 for regulating cell polarity, this claim is highly striking.  

However, to strongly support this conclusion, the authors should first perform a rescue experiment using MARK2 KO cells exogenously expressing MARK2. This step is essential for determining whether the defects observed in MARK2 KO cells are caused by the loss of MARK2 expression, but not by other artificial effects that were accidentally raised during the generation of the present MARK2 KO clone.  

We sincerely thank the reviewer for their insightful suggestion regarding the rescue experiment to confirm that the defects observed in MARK2 KO cells are specifically caused by the loss of MARK2 expression.

To address this, we performed a rescue experiment in MARK2 KO HT1080 cells by exogenously expressing GFP-MARK2. Our results, presented in Supplementary Figures 3C-E, demonstrate that GFP-MARK2 expression successfully restores the localization of CAMSAP2 on the Golgi apparatus in MARK2 KO cells.

These findings strongly support the conclusion that the defects in Golgi architecture and CAMSAP2 Golgi localization are directly attributable to the loss of MARK2 expression, rather than any artificial effects potentially introduced during the generation of the MARK2 KO clone.

We hope these additional experimental results address the reviewer’s concerns and provide robust evidence for the role of MARK2 in regulating Golgi reorientation and wound closure. We are grateful for the reviewer’s constructive feedback, which has significantly improved the rigor and clarity of our study.

In addition, to evaluate the impact of the rescue effect of CAMSAP2, the authors should include the data of wild-type HT1080 and MARK2 KO cells in Fig. 5B to reliably demonstrate the aforementioned claim.  

We thank the reviewer for their valuable suggestion to include data from wild-type HT1080 and MARK2 KO cells in Figure 5A-C to better evaluate the rescue effects of CAMSAP2.

In response, we have incorporated data from wild-type HT1080 and MARK2 KO cells into Figure 5A-C. These additions provide a comprehensive comparison and further demonstrate the impact of CAMSAP2-S835A and CAMSAP2-S835D on Golgi reorientation relative to the wild-type and MARK2 KO conditions.

These changes are reflected in Figures 5A-C.

We hope these updates address the reviewer’s concerns and strengthen the reliability of our conclusions. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the robustness of our study.

Principally, before checking the rescue effects in MARK2 KO cells, the authors should examine the rescue activity of the CAMSAP2 S835 mutants in restoring the reduced reorientation of the Golgi in wound-healing cells and the delay in wound closure observed in CAMSAP2 KO cells (Supplementary Fig.1F-H and Supplementary Fig.2A, B). These experiments are more essential experiments to substantiate the authors' claim.

We thank the reviewer for their insightful suggestion to examine the rescue activity of CAMSAP2 S835 mutants in CAMSAP2 KO cells to further substantiate our claims.

In Figure 4D-F, we observed significant differences between CAMSAP2 S835 mutants in their ability to restore Golgi structure and localization, indicating functional differences between these mutants. To better reflect the regulatory role of MARK2-mediated phosphorylation of CAMSAP2, we performed scratch wound-healing experiments in MARK2 KO cells by establishing stable cell lines expressing CAMSAP2 S835 mutants. These experiments allowed us to assess Golgi reorientation during wound healing and are presented in Figure 5A-C.

We also attempted to generate stable cell lines expressing GFP-CAMSAP2 and its mutants in CAMSAP2 KO cells. Unfortunately, these cells consistently failed to survive, preventing successful construction of the cell lines.

We hope these experiments and explanations address the reviewer’s concerns. We are grateful for the reviewer’s constructive feedback, which has helped us refine and improve our study.

(5) The data presented in Fig. 6A and B are not sufficient to support the authors' notion that "our observation revealed notable changes in the Golgi apparatus and microtubule network distribution in relation to the wounding. (page 11)"  

Fig. 6A, which includes only a single-cell image in each panel, does not demonstrate the general state of microtubules and the Golgi in the wound-edge cells. The reader cannot even know the migration direction of each cell.  

Fig.6 B are not suitable to quantitatively support the authors' claim. The authors should find a way to quantitatively estimate the microtubule density around the Golgi and the shape and compactness of the Golgi in each cell facing the wound, not estimating the colocalization of microtubules and the Golgi, as in the present Fig. 6B.  

We sincerely apologize for the confusion caused by our unclear descriptions and presentation.

Here, we clarify the purpose and improvements made to address the reviewer’s concerns. In this study, we primarily aimed to observe the relationship between microtubules and the Golgi apparatus in cells at the leading edge of the wound during directed migration. In Figure 6A (now Supplementary Figure 6E), the images represent cells located at the wound edge at different time points. To improve clarity, we have added arrows indicating the migration direction and updated the figure legend to describe these details (page 40 lines 13-14).

To better quantify the relationship between microtubules and the Golgi apparatus, we revised our analysis by referring to the quantitative method used in Figure 3F of the paper Molecular Pathway of Microtubule Organization at the Golgi Apparatus. Specifically, we performed a radial analysis of fluorescence intensity in cells at the wound edge, measuring the distance from the Golgi center (x-axis) and the normalized radial fluorescence intensity of microtubules and the Golgi (y-axis). These results are now presented in Supplementary Figure 6E and 6F.

We hope these improvements address the reviewer’s concerns and provide stronger evidence for the changes in the Golgi apparatus and microtubule network distribution in relation to wound healing. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the clarity and rigor of our study.

The legends to Fig. 6A and B indicate that they compared immunofluorescent staining of cells at the edge of the wound after 0.5h and 2 h of migration. However, the authors state in the text that they compared "the cells located before the wound" and "the cells at the trailing edge of the wounding (page 11)."Although this description is highly ambiguous and misleading, if they compared the wound-edge cells and the cells separated from the wound edge at 2 h after cell migration here, they should improve the experimental design as I pointed out in the 2nd major comment.  

We thank the reviewer for their detailed feedback regarding the experimental design and the need to clarify our descriptions. We have addressed these concerns as follows:

- Clarification of descriptions:

We recognize that the previous description in the text regarding "the cells located before the wound" and "the cells at the trailing edge of the wounding" was ambiguous and potentially misleading. We have revised this text to accurately describe the experimental design. Specifically, we compared cells at the leading edge of the wound at different time points (0.5h and 2h post-migration). These corrections are reflected in figure legends (Supplementary Figure 6E and 6F ) and the Results section (page 11,lines 3-8).

- Improved experimental design:

To better support our conclusions, we performed live-cell imaging to observe the dynamic changes in the Golgi apparatus during directed migration. As shown in Supplementary Figure 2A, our results confirm that the Golgi apparatus undergoes a transient dispersed state before reorganizing into an intact structure.

Additionally, we performed fixed-cell staining at different time points to analyze the colocalization of CAMSAP2 with the Golgi apparatus in cells at the leading edge of the wound. The colocalization analysis, presented in Figures 1A-C, further demonstrates the dynamic regulation of CAMSAP2 during Golgi reorientation.

We hope these updates address the reviewer’s concerns and provide a clearer and more robust foundation for our conclusions. We are grateful for the reviewer’s constructive feedback, which has greatly enhanced the clarity and rigor of our study.

Minor comments  

(1) In Fig. 2 and Supplementary Fig. 3, the authors claim that MARK2 is enriched around the Golgi. However, this claim was based on immunofluorescent images of single cells and single-line scans.  

It is better to present the statistical data for Pearson's coefficient as shown in Figs. 1D and E. To demonstrateMARK2 enrichment around Golgi, but not localization in Golgi, the authors should find a way to quantify the specific enrichment of MARK2 signals in the Golgi region.  

We thank the reviewer for raising this important point regarding the enrichment of MARK2 around the Golgi apparatus. Upon further consideration, we acknowledge that our current data do not provide sufficient evidence to fully elucidate the mechanism of MARK2 localization to the Golgi.

To maintain the scientific rigor of our study, we have removed this claim and the corresponding content from the manuscript, including original Figures 2 and Supplementary Figure 3 that specifically discuss MARK2 enrichment. These changes do not affect the primary conclusions of the study, which focus on the role of MARK2-mediated phosphorylation of CAMSAP2.

We hope this clarification addresses the reviewer’s concerns. In the future, we plan to investigate the precise mechanism of MARK2 localization using additional experimental approaches. We are grateful for the reviewer’s constructive feedback, which has helped us refine the scope and focus of our manuscript.

(2) In Fig. 3 and Supplementary Fig. 4, the authors report that CAMSAP2 localization on the Golgi is reduced in cells lacking MARK2.  

Essentially, the present results support this claim. However, the authors should analyze the Golgi localization of CAMASP2 with the same quantification parameter because they used Pearson's coefficient in Fig. 1D, E and Supplementary Fig.4D but Mander's coefficient in Fig. 3C and Fig.4F.  

We thank the reviewer for their insightful comment regarding the consistency of quantification parameters used in our analysis of CAMSAP2 localization on the Golgi apparatus.

To address this concern, we have revised Figure 3C to use Pearson’s coefficient for consistency with Figure 1D, 1E (Figure 1B and 1E in the revised manuscript), and Supplementary Figure 4D (Supplementary Figure 3I in the revised manuscript). This ensures uniformity in the quantification parameters across these analyses.

For Figure 4F, we have retained Mander’s coefficient, as it accounts for variability in expression levels due to overexpression in individual cells. We believe this approach provides a more accurate reflection of CAMSAP2 localization under the experimental conditions shown in Figure 4F.

We hope these adjustments clarify our analysis and address the reviewer’s concerns. We greatly appreciate the reviewer’s constructive feedback, which has helped improve the consistency and accuracy of our study.

(3) In Fig.4D-F, the authors claim that S835 phosphorylation of CAMSAP2 is essential for its localization to the Golgi apparatus and for restoring the Golgi dispersion induced by CAMASAP2 depletion.  

Fig.4E indicates that the S835A mutant of CAMSAP2 significantly restores the compact assembly of the Golgi apparatus, and the differences in the rescue activities of the wild type, S835A, and S835D are rather small. These data contradict the authors' conclusions regarding the pivotal role of MARK2-mediated phosphorylation at the S835 site of CAMSAP2 in maintaining the Golgi architecture (page 9). The authors should remove the phrase "MARK2-mediated" from the sentence unless addressing the aforementioned issues (see 3rd major comment) and describe the role of S835 phosphorylation in more subdued tone.  

We thank the reviewer for their constructive feedback regarding the conclusions drawn about the role of MARK2-mediated phosphorylation of CAMSAP2 at S835.

In response, we have revised the relevant sentence to reflect a more nuanced interpretation of the data. Specifically, the original statement:

“These observations indicate that the phosphorylation of serine 835 in CAMSAP2 is essential for its proper localization to the Golgi apparatus.”

has been updated to:

“These observations indicate that MARK2 phosphorylation of serine at position 835 of CAMSAP2 affects the localization of CAMSAP2 on the Golgi and regulates Golgi structure” (page 9, Lines 27-29).

We hope this modification addresses the reviewer’s concerns. We are grateful for the feedback, which has helped us refine our conclusions and enhance the clarity of our manuscript.

(4) In Figs. 5I, J and Supplementary Fig.7A-E, the authors claim that the S835 phosphorylationdependent interaction of CAMSAP2 with Uso1 is essential for its localization to the Golgi apparatus.  

This claim was made based on immunofluorescent images of single cells and single-line scans, and was not sufficiently verified (Supplementary Fig.7B, C). Because this is a crucial claim for the present paper, the authors should present statistical data for Pearson's coefficient, as shown in Fig. 1D and E, to quantitatively estimate the Golgi localization of CAMSAP2.  

We thank the reviewer for their suggestion to present statistical data using Pearson's coefficient for a more robust quantification of the Golgi localization of CAMSAP2.

In response, we have revised the statistical analysis for Supplementary Figures 7B-C (Revised Figures 6F and 6G) to use Pearson's coefficient. This change ensures consistency with the quantification methods used in Figures 1D and 1E (Revised Figures 1B and 1E), allowing for a more standardized evaluation of CAMSAP2’s localization to the Golgi apparatus.

We hope this modification addresses the reviewer’s concerns and strengthens the quantitative support for our claims. We are grateful for the reviewer’s constructive feedback, which has helped improve the rigor of our study.

(5) The signal intensities of the immunofluorescent data in Fig. 4D, Fig. 5A, Sup-Fig. 3C and E, and Sup-Fig. 7S are very weak for readers to clearly estimate the authors' claims. They should be improved appropriately.  

We thank the reviewer for highlighting the need to improve the clarity of the immunofluorescent data presented in several figures.

In response, we have enhanced the signal intensities in Figures 4D, 5A, and Supplementary Figure 7D (Revised Supplementary Figure 6A) to make the signals clearer for readers, while ensuring that the adjustments do not alter the integrity of the original data. Supplementary Figures 3C and 3E was remove from our manuscript.

Additionally, to improve consistency and readability across the manuscript, we have standardized the quantification methods for similar analyses:

For CAMSAP2 localization to the Golgi, Pearson's coefficient has been used throughout the manuscript. Figure 3C has been updated to use Pearson's coefficient for consistency.

For Golgi state analysis in wound-edge cells, we have used the Golgi position relative to the nucleus as a uniform metric. This has been applied to Supplementary Figures 1F and 1G, Figures 2D and 2E, and Figures 5A and 5B.

We hope these adjustments address the reviewer’s concerns and improve the clarity and consistency of our study. We greatly appreciate the reviewer’s constructive feedback, which has significantly enhanced the quality of our manuscript.

(6) As indicated above, the authors frequently change the parameters or methods for quantifying the same phenomena (for example, the localization of CAMSAP on the Golgi and Golgi state in wound edge cells) in each figure. This is highly confusing. They should unify them.  

We thank the reviewer for their valuable feedback regarding the inconsistency in quantification methods across the manuscript.

To address this concern, we have carefully reviewed the entire manuscript and standardized the methods used for quantifying similar phenomena:

- CAMSAP2 localization on the Golgi: 

Pearson's coefficient is now consistently used throughout the manuscript. For example, Figure 3C has been updated to use Pearson's coefficient to align with other figures, such as Figures 1B and 1E.

- Golgi state in wound-edge cells: 

The Golgi state is now uniformly measured based on the position of the Golgi relative to the nucleus. This method has been applied to Supplementary Figures 1F and 1G, Figures 2D and 2E, and Figures 5A and 5B.

We believe these changes significantly improve the clarity and consistency of the manuscript, ensuring that readers can easily interpret the data. We are grateful for the reviewer’s constructive feedback, which has greatly helped us enhance the quality and rigor of our study.

(7) The legends frequently fail to clearly indicate the number of independent experiments on which each statistical analysis was based.  

We thank the reviewer for highlighting the need to clearly indicate the number of independent experiments for each statistical analysis.

In response, we have carefully reviewed the entire manuscript and updated the figure legends to include the number of independent experiments for every statistical analysis. This ensures transparency and allows readers to better evaluate the reliability of the data.

We hope these updates address the reviewer’s concerns and improve the clarity and rigor of the manuscript. We appreciate the reviewer’s constructive feedback, which has helped us enhance the quality of our work.

(8) Supplemental Figs. 4E and 4F are not cited in the text.  

We thank the reviewer for pointing out that Supplemental Figures 4E and 4F were not cited in the text.

To address this, we have updated the manuscript to cite these figures (Revised Figures 2H and 2I) in the appropriate section (page 8, lines 1-5).

“the absence of MARK2 can also influence the orientation of the Golgi apparatus during cell wound healing and cause a delay in wound closure (Figure 2 D-I and Figure 3 D).”

We hope this revision resolves the reviewer’s concern and improves the clarity and completeness of the manuscript. We appreciate the reviewer’s feedback, which has helped us refine our work.

(9) The data in Fig. 3 analyzed MARK2 knockout cells (not knockdown cells). The caption should be corrected.  

We thank the reviewer for pointing out the incorrect use of "knockdown" in the caption of Figure 3.

To address this, we have revised the title of Figure 3 from:

“MARK2 knockdown reduces CAMSAP2 localization on the Golgi apparatus.”

to:

“MARK2 affects CAMSAP2 localization on the Golgi apparatus.”

This updated caption reflects the inclusion of both MARK2 knockout and knockdown cell lines analyzed in Figure 3.

We hope this correction resolves the reviewer’s concern and ensures the accuracy of our manuscript. We greatly appreciate the reviewer’s attention to detail, which has helped us improve the clarity and consistency of our work.

(10) The present caption in Fig. 6 disagrees with the content of the figure.  

We thank the reviewer for pointing out the inconsistency between the caption and the content of Figure 6.

To address this issue, we have revised the content of Figure 6 to ensure it aligns accurately with the caption. The updated figure now reflects the description provided in the caption, eliminating any discrepancies and improving clarity for the readers.

We appreciate the reviewer’s constructive feedback, which has helped us enhance the accuracy and presentation of our manuscript.

(11) What do "CS" indicate in Fig. 4B and Supplementary Fig. 5D? The style used to indicate point mutants of CAMSAP2 should be unified. 835A or S835A?  

We thank the reviewer for pointing out the inconsistency in the naming of CAMSAP2 mutants.

To address this, we have revised all relevant figures and text to use the consistent format "S835A" and "S589A" for CAMSAP2 mutants. Specifically, in Figure 4B and Supplementary Figure 5D (now Supplementary Figure 4C), we have replaced the abbreviation "CS2" with "CAMSAP2" and updated the mutant names from "835A" and "589A" to "S835A" and "S589A," respectively. We hope these updates resolve the reviewer’s concerns and ensure clarity and consistency throughout the manuscript. We are grateful for the reviewer’s attention to detail, which has helped us improve the quality of our work.

(12) Uso1 is not a Golgi matrix protein.  

We thank the reviewer for pointing out the incorrect description of Uso1 as a Golgi matrix protein.

In response, we have revised the manuscript to replace all references to “USO1 as a Golgi matrix protein” with “USO1 as a Golgi-associated protein.” This correction ensures that the terminology used in the manuscript is accurate and consistent with current scientific understanding.

We appreciate the reviewer’s attention to detail, which has helped us improve the accuracy and quality of our manuscript.

Author response:

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

Reviewer #1 (Public review):

Summary:

In this manuscript, De La Forest Divonne et al. build a repertory of hemocytes from adult Pacific oysters combining scRNAseq data with cytologic and biochemical analyses. Three categories of hemocytes were described previously in this species (i.e. blast, hyalinocyte, and granulocytes). Based on scRNAseq data, the authors identified 7 hemocyte clusters presenting distinct transcriptional signatures. Using Kegg pathway enrichment and RBGOA, the authors determined the main molecular features of the clusters. In parallel, using cytologic markers, the authors classified 7 populations of hemocytes (i.e. ML, H, BBL, ABL, SGC, BGC, and VC) presenting distinct sizes, nucleus sizes, acidophilic/basophilic, presence of pseudopods, cytoplasm/nucleus ratio and presence of granules. Then, the authors compared the phenotypic features with potential transcriptional signatures seen in the scRNAseq. The hemocytes were separated in a density gradient to enrich for specific subpopulations. The cell composition of each cell fraction was determined using cytologic markers and the cell fractions were analysed by quantitative PCR targeting major cluster markers (two per cluster). With this approach, the authors could assign cluster 7 to VC, cluster 2 to H, and cluster 3 to SGC. The other clusters did not show a clear association with this experimental approach. Using phagocytic assays, ROS, and copper monitoring, the authors showed that ML and SGC are phagocytic, ML produces ROS, and SGC and BGC accumulate copper. Then with the density gradient/qPCR approach, the authors identified the populations expressing anti-microbial peptides (ABL, BBL, and H). At last, the authors used Monocle to predict differentiation trajectories for each subgroup of hemocytes using cluster 4 as the progenitor subpopulation.

The manuscript provides a comprehensive characterisation of the diversity of circulating immune cells found in Pacific oysters.

Strengths:

The combination of the two approaches offers a more integrative view.

Hemocytes represent a very plastic cell population that has key roles in homeostatic and challenged conditions. Grasping the molecular features of these cells at the single-cell level will help understand their biology.

This type of study may help elucidate the diversification of immune cells in comparative studies and evolutionary immunology.

Weaknesses:

The study should be more cautious about the conclusions, include further analyses, and inscribe the work in a more general framework.

Reviewer #1 (Recommendations for the authors):

The manuscript provides a comprehensive characterisation of the diversity of circulating immune cells found in Pacific oysters.

Major comments:

(1) The introduction would benefit from a clear description of what is known about immune cell development and diversity in this model. The bibliography on the three subtypes origins and properties (i.e. blast, hyalinocyte, and granulocytes) should be described in the introduction.

We thank Reviewer #1 for their valuable comments, which have allowed us to further improve our manuscript. We have enriched the introduction with the following addition (line 79 to 82):

“Blast-like cells are considered as undifferentiated hemocyte types (20), hyalinocytes (21) seem to be more involved in wound repair, and granulocytes, more implicated in immune surveillance. The latter are considered as the main immunocompetent hemocyte types (22).”

(2) The authors mentioned a previous scRNAseq dataset produced in another oyster species. They should compare the two datasets to show the robustness of the molecular signatures determined in the present study. In addition, the authors do not mention markers identified in the literature that could be relevant to characterize the clusters (e.g. inflammatory pathway PMID: 29751033, proliferative markers PMID: 36591234/ PMID: 29317231, granulocyte markers PMID: 30633961 ... list not exhaustive). Overall, the comparison of this manuscript dataset and the available literature is too partial

We appreciate the reviewer’s suggestion to compare our dataset with previously published scRNAseq data and to integrate markers from the literature. Below, we address these points in detail.

The transcription factors involved in hematopoiesis, such as Tal1, Sox, Runx, and GATA, are highly conserved across metazoans. These markers were identified in our dataset, consistent with findings in other species (1–3), including the previously mentioned scRNA-seq dataset in C. hongkongensis (4). However, defining robust and specific markers for distinct hemocyte types remains an ambitious goal that requires validation across diverse biological contexts - work that is beyond the scope of the present study. Additionally, meaningful comparisons between datasets are constrained by differences in annotation frameworks and the absence of a standardized system for defining hemocyte subtypes. These limitations underscore the need for harmonization efforts to facilitate robust cross-study comparisons. Nonetheless, our dataset provides a strong foundation for future comparative analyses once such standardization is achieved.

In response to the reviewer’s comment, we have added a paragraph to the discussion (lines 747 - 760) detailing that we identified conserved transcription factor markers in C. gigas and C. hongkongensis.

(3) The authors sequenced 3000 cells without providing more comprehensive information/rationale on the analysed population. What is the number of hemocytes found in an adult? What proportion of the whole hemocyte population does this analysis represent? Does it include the tissue-interacting hemocytes? Also, what is the rationale for choosing that specific stage?

We thank the reviewer for their insightful questions regarding the analyzed hemocyte population.

Adult 18-month-old Crassostrea gigas contain approximately 1 million circulating hemocytes per mL of hemolymph, with an average of 1 mL of hemolymph per individual. Thus, this represents approximately 1 million circulating hemocytes per oyster. For our scRNA-seq analysis, we sampled 3,000 hemocytes, which corresponds to 0.3% of the total circulating hemocyte population.

The number of cells processed was optimized to minimize the occurrence of doublets during scRNAseq. Following 10x Genomics Chromium guidelines, we loaded 4,950 cells to successfully recover a target of 3,000 cells, with a doublet rate of 2.4%, well below the target threshold of 2.5%. This information has been added on line 125 of the document. The target was 3,000 cells, and as reported in Supplementary Table S1, the estimated number of cells after STAR-solo alignment was 2,937. This ensures the reliability and accuracy of single-cell transcriptomic data.

We selected 18-month-old oysters for two key reasons: (i) to facilitate hemolymph collection, as hemocyte counts are more stable and sufficient at this stage, enabling us to collect enough cells for all planned experiments, including functional and cytological analyses; and (ii) to use oysters that are not susceptible to OsHV-1 μVar herpesvirus, which predominantly affects younger animals. This ensured that the hemocyte populations analyzed were not influenced by viral infections or related immune responses.

Our study focused on circulating hemocytes collected from hemolymph, which does not include tissue-interacting hemocytes. While these cells may represent an additional population of interest, they fall outside the scope of our current investigation.

By carefully selecting the animal stage and optimizing cell sampling, we ensured that the scRNA-seq dataset provides a robust representation of circulating hemocyte diversity while maintaining high data quality.

(4) For the GO term enrichment analysis, the authors included all genes presenting a cluster enrichment above L2FC>0.25. This seems extremely low to find distinct functions for each cluster. The risk is to call "cluster specific GO term" GO terms for which the genes are poorly enriched in the cluster. For the most important GO term mentioned in the text, the authors should show the expression levels of the genes (with DotPlot similar to Fig1D) to illustrate the specificity of the GO term. At last, the GO enrichment scores were apparently calculated using the whole genome as background. The analysis, aiming at finding differences between hemocyte subgroups, should use the genes detected in the dataset as background.

We appreciate the reviewer's concerns regarding the threshold used for GO term enrichment analysis and the choice of background genes. Below, we provide clarification on these points.

For nuanced comparisons, such as those between activation states of the same cell type, lower thresholds for log2FC (e.g., ≥0.25) are commonly used to detect subtle regulatory shifts. In single-cell RNA sequencing (scRNA-seq) analyses, it is typical to use a log2FC threshold between 0.25 and 0.5 to ensure that biologically relevant, yet subtle, changes are captured. For our analysis, this threshold was chosen to maintain sensitivity to such shifts, particularly given the diversity and functional specialization of hemocyte clusters.

To address the reviewer's suggestion, we will include DotPlot representations (similar to Fig. 1D) for the most significant GO terms highlighted in the text. This will illustrate the expression levels of the associated genes across clusters and demonstrate their specificity to the identified GO terms.

Regarding the background used in the GO enrichment analysis, we employed the Rank Based Gene Ontology Analysis (RBGOA) approach, which explicitly states in its documentation: "It is important to have the latter two tables representing the whole genome (or transcriptome) — at least the portion that was measured — rather than some select group of genes since the test relies on comparing the behavior of individual GO categories to the whole." Our analysis was conducted in agreement with these initial recommendations, ensuring that the results are consistent with the methodology outlined for RBGOA.

(5) The authors reannotated the genes of C. gigas to reach 73.1% annotation. What are the levels of annotations found prior to the reannotation? What do the scores/scale bars from the RBGOA analysis mean in Figures 2B-D?

Thank you for your comment. The original annotation for C. gigas was based on the work of Penaloza et al. (5), which provided GO annotations for 18,750 out of 30,724 genes, corresponding to 61% annotation. Following our reannotation efforts, we were able to increase the annotation coverage to 73.1%, enhancing the resolution of downstream analyses. In response to the reviewer’s comment, we have updated the results section (line 211 and 216) to explicitly include the original annotation coverage of 61% from the work of Penaloza et al., followed by details on our newly achieved annotation percentage of 73.1%.

Thank you for pointing this out. We apologize for the oversight regarding the scale bar in Figures 2BD. The colors in the original figure correspond to a z-score calculated from the gene ratio, which was not clearly explained and may have caused confusion. In the revised version of the manuscript, we propose a new representation to facilitate understanding and improve the clarity of the data presentation (Figure 2B).

(6) The authors describe first the result of the Kegg enrichment analysis and then of the RBGOA. To gain fluidity, I would suggest merging the results of both Kegg and RBGOA for each cluster.

Thank you for the suggestion. To enhance the fluidity of the results section, we have redesigned the KEGG/RBGOA figure (see figure 2A and 2B) to present the results for each cluster in an integrated manner. This revised approach aims to provide a clearer and more cohesive representation of the findings.

(7) The authors make correlations between gradient fraction containing multiple hemocyte populations and qPCR expression levels of cluster-specific markers to associated cytologic features with specific clusters. If feasible, I would recommend validating the association of several markers with hemocyte subgroups using in situ hybridisation or immunolabelling.

Cytological identification of hemocytes in our study relies on MCDH staining, which provides detailed morphological and cytological information. Unfortunately, the fixation methods required for in situ hybridization (ISH) or immunolabeling are not compatible with those used for MCDH staining. We attempted to combine these approaches but found that the fixation protocols necessary for ISH or immunolabeling compromised the quality of the cytological features observed with MCDH staining. Consequently, such validation was not feasible within the constraints of our experimental setup.

(8) Anti-microbial peptides are mentioned as enriched in agranular cells based on the gradient/qPCR analysis (Figure 6). Are these AMPs regulated by inflammatory pathways? Are any inflammatory pathways enriched in any scRNAseq cluster? In addition, without validating the data by directly labelling AMP in the different populations, it seems hard to conclude that AMP are expressed only by agranular cells.

In oysters, two families of antimicrobial peptides/proteins appear to be transcriptionally regulated in hemocytes in response to an infection. The first is that of Cg-BigDefs (6). A 2020 article indicates that the expression of CgBigDef1 is regulated by CgRel, an ortholog of the NFkB transcription factor, which also control the expression of the proinflammatory cytokine CgIL17 (7). Cg-BPI is induced in response to infection but its regulatory pathways remain unknown (8). The last well characterized family of antimicrobial peptides is Cg-Defs. It exhibits constitutive expression in hemocytes.

In our scRNA-seq analysis, CgRel (G12420) shows an increased expression in cluster 5, with a log2FC of 0.4 (equivalent to a 1.32-fold change or 32% higher expression compared to other clusters). Cluster 5 corresponds to blast-like cells, which are transcriptionally distinct and predominantly found in fractions 1, 2, and 3. These same fractions exhibit the highest CgBigDef expression, as demonstrated by qPCR.

From our qPCR results, we see no expression of the three AMP families in cell-sorted granular cells while the cell-sorted agranular cells are positive for the three AMP families, even for inducible ones. Still, we agree that labelling of cell sorted hemocyte populations would reinforce our data. We now specify in the text that further staining would be necessary to confirm these transcriptomic results (Discussion, lines 695 to 296).

(9) The authors should play down some statements concerning cluster identity. In the absence of a true lineage tracing approach, it is possible that those clusters represent states rather than true cell subtypes. Immune cells are very plastic in nature and able to adapt to the environment, even in conditions that are considered homeostatic.

We appreciate the reviewer’s insightful comment regarding the plasticity of immune cells and the potential for clusters to represent states rather than distinct cell subtypes. We agree that, in the absence of a lineage tracing approach, definitive classification of clusters as fixed subtypes is challenging. Immune cells, including those in invertebrates, are known for their high degree of plasticity and adaptability to environmental cues.

In response to the reviewer’s comment, we have revised the Discussion section to include a statement clarifying that these clusters may represent dynamic states rather than fixed subtypes, thereby acknowledging the plasticity of immune cells (lines 766 to 770).

(10) Related to the above issue, there is no indication of stem cells being present in the cell population. Is there any possibility to look for proliferative or progenitor markers? In homeostatic and in challenged conditions (for example Zymosan treatment)? This would provide some hints into the cellular pathways involved in the response. Perhaps determining the number/fraction of phagocytic cells in challenged conditions would help as well, in the absence of time-lapse assays.

Thank you for highlighting the possibility of stem cells or progenitor markers in our hemocyte populations. In our current analysis, we did not detect any known stem cell or proliferative markers, nor evidence of a clearly defined hematopoiesis site in the hemolymph. Indeed, previous work suggests that oyster hematopoiesis may occur in tissues such as the gills, implying that stem or progenitor cells might not circulate in the hemolymph under homeostatic conditions. Consequently, it is plausible that our observation of no proliferative cell populations partly reflects their absence in hemolymph, especially in naïve (unstimulated) oysters. To conclusively identify potential progenitor cells and their proliferative activity, further approaches involving deliberate perturbation of hemocyte homeostasis - such as immunological challenge (e.g., Zymosan treatment) combined with lineagetracing or proliferation assays - would be necessary. These future investigations would not only clarify whether proliferative cells emerge in the hemolymph in response to environmental or pathological stimuli but also help elucidate the broader cellular pathways underlying oyster immune responses.

In response to the reviewer’s comment, we have revised the Discussion (lines 742 to 745) and added : “Nevertheless, we did not detect any canonical stem or progenitor cell populations in our dataset, underscoring the need for future investigations - potentially involving immunological challenges and lineage-tracing assays - to clarify whether proliferative cells circulate in the hemolymph or instead reside primarily in tissue compartments.”

(11) Could the authors discuss the phagocytic hemocytes in light of scavenger receptor expression?

We thank the reviewer for this insightful question. Our study identifies macrophage-like cells and small granule cells as the principal phagocytes in Crassostrea gigas, capable of robust pathogen engulfment. Transcriptomic data reveal that these cell types express markers associated with endocytosis and immune defense pathways, such as CLEC and LACC24, which are integral to their phagocytic functionality.

Interestingly, our single-cell RNA sequencing analysis indicates that cluster 3, corresponding to small granule cells, expresses the scavenger receptor cysteine-rich (SRCR) gene G3876, annotated as an Low-density lipoprotein receptor-related protein with a Log2 fold change (Log2FC) of 0.77. This finding directly links small granule cells to scavenger receptor-mediated functions, supporting their role as professional phagocytes. Scavenger receptors, including SRCR proteins, are known for their ability to bind and internalize diverse ligands, including pathogens, and their presence in small granule cells highlights a potential mechanism for pathogen recognition and clearance.

Additionally, scavenger receptors are significantly expanded in oysters, as shown in Wang et al. (9). These receptors exhibit dynamic upregulation in hemocytes upon pathogen exposure, particularly following stimulation with pathogen-associated molecular patterns (PAMPs) such as lipopolysaccharide (LPS). This evidence suggests that SRCR proteins, including the one identified in our study, play a pivotal role in the phagocytic activities of hemocytes by facilitating pathogen recognition and internalization.

We propose to add this paragraph (lines 610 to 618) in the Discussion : “Interestingly, our scRNA-seq analysis indicates that SGC (cluster 3) expresses the scavenger receptor cysteine-rich (SRCR) gene G3876, annotated as an Low-density lipoprotein receptor-related protein with a Log2 fold change (Log2FC) of 0.77 linking them to scavenger receptor-mediated pathogen recognition and clearance. This aligns with findings by Wang et al. (9), who demonstrated significant expansion and dynamic regulation of SRCR genes in response to pathogen-associated molecular patterns. “

(12) I am not convinced by the added value of the lineage analysis and the manuscript could stand without it. There is no experimental validation to substantiate the filiation between the clusters. In addition, rooting the lineage to cluster 4 is poorly justified (enrichment in the ribosomal transcript). Cluster 6 is also enriched in ribosomal transcripts and this enrichment can be caused by the low threshold used for the selection of cluster-specific genes (L2FC >0.25). At last, cluster 4 > VC and cluster 4 >SGC belong to the same lineage according to Figure 7 FH.

We thank the reviewer for their detailed comments regarding the lineage analysis. We acknowledge the limitations in experimentally validating the proposed filiation between clusters, as hemocytes in Crassostrea gigas cannot currently be cultivated ex-vivo, and we lack the ability to isolate cells specifically from cluster 4 for further functional assays. Consequently, our lineage analysis is based solely on transcriptomic data and pseudo-time trajectory analysis.

Hematopoietic stem cells (HSCs) are a population of stem cells that are largely cell-cycle-quiescent (G0 phase) with low biosynthetic activity. Upon stimulation and stress HScs undergo proliferation and differentiation and produce all lineages of hemocytes.

Ribosomal proteins play a multifaceted role in preserving the balance between stem cell quiescence and activation. By ensuring precise regulation of protein synthesis, they allow stem cells to maintain their undifferentiated state while remaining poised for activation when needed. Furthermore, ribosomal proteins contribute to the cellular stress response, safeguarding stem cells from oxidative damage and other stressors that could compromise their functionality. Importantly, ribosomal biogenesis and the dynamic assembly of ribosomes provide a regulatory mechanism that fine-tunes the transition from self-renewal to differentiation, a critical feature of hematopoietic stem cells (HSCs) and other stem cell types. These mechanisms collectively highlight the indispensable role of ribosomal proteins in stem cell biology, underscoring their relevance to our study's findings.

In vertebrate, the maintenance of hematopoietic stem cells (HSCs) and hematopoietic homeostasis is widely acknowledged to rely on the proper regulation of ribosome function and protein synthesis (10). This process necessitates the coordinated expression of numerous genes, including genes that encode ribosomal proteins (RP genes) and those involved in regulating ribosome biogenesis and protein translation. Disruptions or mutations in these critical genes are associated with the development of congenital disorders (11). Among these, Rpl22 (found in cluster 4 with a Log2FC of 1.59) has been shown to play a pivotal role in HSC maintenance by balancing ribosomal protein paralog activity, which is critical for the emergence and function of HSCs (12).

Regarding the justification for rooting the lineage to cluster 4, our decision was informed by the enrichment of ribosomal transcripts and functional annotations suggesting a role in translation and cell proliferation, consistent with a precursor-like state. The use of a log2 fold-change (L2FC) threshold of >0.25, while conservative, allowed us to include subtle but meaningful transcriptional shifts essential for resolving lineage transitions.

Finally, the lineage progression from cluster 4 to vesicular cells (VC), macrophage-like cells (ML), and ultimately small granule cells (SGC) is supported by trajectory analysis (Figure 7FH), which consistently places VC and ML as intermediates in the differentiation process toward SGC. Although experimental validation is currently not feasible, these findings provide a conceptual framework for future investigations when cell isolation and functional validation tools become available.

(13) The figures containing heatmaps (Figure 7, Figure 2, Figure S10) or too many subpanels (Figure S5) and Table S5 are hardly readable.

Thank you for highlighting the issues related to the clarity of the heatmaps (Figures 2, 7, and S10), the multi-panel figure (Figure S5), and Table S5. In response to your feedback, we have revised all of these elements to enhance readability and comprehension. Specifically, we increased font sizes, optimized color scales, and reorganized the layout of the subpanels to emphasize the key findings. We also updated Table S5 to ensure that the data are presented in a clear and easily interpretable format.

We trust that these modifications address the concerns raised and improve the overall clarity of the figures and table.

(14) A number of single-cell analyses are now available in different species and the authors allude to similar pathways/transcription factors being involved. Perhaps the authors could expand on this in the discussion section.

Transcription factors involved in hematopoiesis, such as Tal1, Runx and GATA, are highly conserved across metazoans. Consistent with findings in other species, our dataset identifies these markers, reinforcing the evolutionary conservation of these pathways. Furthermore, these markers are also reported in the previous scRNA-seq dataset for C. hongkongensis (4), supporting the robustness of our molecular signatures. However, defining specific and robust markers for distinct hemocyte types remains an ambitious task, requiring additional validation in diverse biological and experimental contexts. This validation is beyond the scope of the present study.

In addition, meaningful comparisons between scRNA-seq datasets are constrained by differences in annotation frameworks and the absence of standardized definitions for hemocyte subtypes. Harmonizing these datasets to enable robust cross-species comparisons is a critical challenge for future studies. Nonetheless, the insights provided by our dataset establish a strong foundation for such comparative analyses when these standardization efforts are realized.

In crayfish (1), 16 transcriptomic clusters were identified corresponding to three hemocyte types, with markers such as integrin prominently expressed in hyalinocytes, consistent with our identification of integrin-related genes in hemocytes. In shrimp (1), 11 transcriptomic clusters were described, with markers of hemocytes in immune-activated states, that we observed also in our dataset. For Anopheles gambiae (2), 8 transcriptomic clusters were identified, including clusters with high ribosomal activity, analogous to those we described in our study. Finally, in Bombyx mori (3), 20 transcriptomic clusters were reported, corresponding to five cytological hemocyte types. Transcription factors such as bHLH, myc, and runt were identified in granulocytes and oenocytoid, showing parallels with markers identified in our dataset.

Despite these similarities, cross-species comparisons are hindered by variability in genome availability and annotation quality, which complicates the precise identification and functional characterization of genes across datasets. Notably, we did not detect pro-phenoloxidase genes in our dataset, unlike shrimp and crayfish, suggesting potential species-specific differences in immune mechanisms.

Regarding the previously published C. hongkongensis scRNA-seq dataset (4), we observe overlap in markers such as runx and GATA. However, direct comparisons remain limited due to differences in dataset annotations and definitions of hemocyte subtypes. This underscores the need for standardized frameworks to facilitate cross-study comparisons. While we emphasize that robust cross-species validation was beyond the scope of this study, our findings contribute valuable insights into the molecular signatures of oyster hemocytes and provide a framework for future comparative research.

We have expanded our discussion to include comparisons with available scRNAseq data from other invertebrate specie (lines 747 to 760)

Minor comments:

(1) Figure 2A-D: to increase the readability of the figure, the authors should display only the GO terms mentioned in the text and keep the full list in supplementary data.

To enhance the fluidity of the results section, we have redesigned the KEGG/RBGOA figure to present the results for each cluster in an integrated manner (See figure 2A and 2B).

(2) Line 223: the authors mention that cluster 1 is characterized by its morphology without providing an explanation or evidence.

We have revised the description of Cluster 1 to remove references to morphology, ensuring consistency with the data presented at this stage of the manuscript (lines 227 to 229) : ”Cluster 1, comprising 27.6 % of cells, is characterized by GO-terms related to myosin complex, lamellipodium, membrane and actin cytoskeleton remodelling, as well as phosphotransferase activity.”

(3) Line 306: the authors mentioned expression levels and associated them with Log2FC, which represents an enrichment, not the level of expression.

Thank you for pointing this out. We agree that log2FC represents enrichment rather than absolute expression levels. We have revised the text in the manuscript to clarify this distinction (line 309). The corrected text now states that log2FC reflects the degree of enrichment or depletion of a gene in a specific cluster relative to others, rather than its absolute expression level.

(4) Figure 4B: the figure shows the distribution of all hemocytes subgroups for each fraction. To better appreciate the distribution of the subgroups in the different fractions, it would be good to have the number of cells of each subtype in the fractions.

We thank the reviewer for their suggestion to include the number of cells of each subtype in the fractions. While we do not have the exact total number of cells per fraction, we systematically performed hemocyte counts for each fraction as part of our methodology. These counts provide a robust estimation of hemocyte distributions across fractions.

Including these counts in the figure could be an alternative approach; however, we believe it would not significantly enhance the interpretability of the data, as the focus of this analysis is on the relative proportions of hemocyte subtypes rather than absolute numbers. The current representation provides a clear and concise overview of subtype distribution patterns, which aligns with the goals of the study.

Nevertheless, if the reviewer considers it essential, we are open to integrating the hemocyte counts into the figure or supplementing the information in the text or supplementary materials to provide additional context.

(5) Line 487-488: the authors mentioned that monocle 3 can deduce the differentiation pathway from the mRNA splice variant. I did not find this information in the publication associated with the statement.

Thank you for pointing this out. We acknowledge the inaccuracy in our statement regarding Monocle3's capabilities. Monocle3 does not deduce differentiation pathways based on mRNA splice variants, as was erroneously suggested in the manuscript. Instead, Monocle3 performs trajectory inference using gene expression profiles. It calculates distances between cells based on their transcriptomic profiles, where cells with similar profiles are positioned closer together, and those with distinct profiles are farther apart. This method enables the construction of potential differentiation trajectories by identifying paths between transcriptionally related cells.

We revise the text in the manuscript to accurately describe this process and remove the incorrect reference to mRNA splice variants (lines 495 to 497).

(6) Figures 6C-H display heatmaps with two columns representing the beginning and the end of the lineage predicted. It would be more talkative to show the whole path presented in Figure S10.

Thank you for pointing out that Figures 7C–H currently only show the beginning and end of the predicted lineage, limiting the clarity of the intermediate stages. In response to your suggestion, we have revised these figures to include the full trajectory as presented in Figure S10, ensuring that the intermediate transitions are more clearly visualized. We believe these modifications offer a more comprehensive overview of the entire lineage and enhance the interpretability of our results.

Bibliography:

(1) F. Xin, X. Zhang, Hallmarks of crustacean immune hemocytes at single-cell resolution. Front. Immunol. 14 (2023).

(2) H. Kwon, M. Mohammed, O. Franzén, J. Ankarklev, R. C. Smith, Single-cell analysis of mosquito hemocytes identifies signatures of immune cell subtypes and cell differentiation. eLife 10, e66192 (2021).

(3) M. Feng, L. Swevers, J. Sun, Hemocyte Clusters Defined by scRNA-Seq in Bombyx mori: In Silico Analysis of Predicted Marker Genes and Implications for Potential Functional Roles. Front. Immunol. 13 (2022).

(4) J. Meng, G. Zhang, W.-X. Wang, Functional heterogeneity of immune defenses in molluscan oysters Crassostrea hongkongensis revealed by high-throughput single-cell transcriptome. Fish & Shellfish Immunology 120, 202–213 (2022).

(5) C. Peñaloza, A. P. Gutierrez, L. Eöry, S. Wang, X. Guo, A. L. Archibald, T. P. Bean, R. D. Houston, A chromosome-level genome assembly for the Pacific oyster Crassostrea gigas. GigaScience 10, giab020 (2021).

(6) R. D. Rosa, A. Santini, J. Fievet, P. Bulet, D. Destoumieux-Garzón, E. Bachère, Big Defensins, a Diverse Family of Antimicrobial Peptides That Follows Different Patterns of Expression in Hemocytes of the Oyster Crassostrea gigas. PLOS ONE 6, e25594 (2011).

(7) Y. Li, J. Sun, Y. Zhang, M. Wang, L. Wang, L. Song, CgRel involved in antibacterial immunity by regulating the production of CgIL17s and CgBigDef1 in the Pacific oyster Crassostrea gigas. Fish & Shellfish Immunology 97, 474–482 (2020).

(8) Evidence of a bactericidal permeability increasing protein in an invertebrate, the Crassostrea gigas Cg-BPI | PNAS. https://www.pnas.org/doi/abs/10.1073/pnas.0702281104.

(9) L. Wang, H. Zhang, M. Wang, Z. Zhou, W. Wang, R. Liu, M. Huang, C. Yang, L. Qiu, L. Song, The transcriptomic expression of pattern recognition receptors: Insight into molecular recognition of various invading pathogens in Oyster Crassostrea gigas. Developmental & Comparative Immunology 91, 1–7 (2019).

(10) R. A. J. Signer, J. A. Magee, A. Salic, S. J. Morrison, Haematopoietic stem cells require a highly regulated protein synthesis rate. Nature 509, 49–54 (2014).

(11) A. Narla, B. L. Ebert, Ribosomopathies: human disorders of ribosome dysfunction. Blood 115, 3196–3205 (2010).

(12) Y. Zhang, A.-C. E. Duc, S. Rao, X.-L. Sun, A. N. Bilbee, M. Rhodes, Q. Li, D. J. Kappes, J. Rhodes, D. L. Wiest, Control of Hematopoietic Stem Cell Emergence by Antagonistic Functions of Ribosomal Protein Paralogs. Developmental Cell 24, 411–425 (2013).

Reviewer #2 (Public review):

Summary:

This work provides a comprehensive understanding of cellular immunity in bivalves. To precisely describe the hemocytes of the oyster C. gigas, the authors morphologically characterized seven distinct cell groups, which they then correlated with single-cell RNA sequencing analysis, also resulting in seven transcriptional profiles. They employed multiple strategies to establish relationships between each morphotype and the scRNAseq profile. The authors correlated the presence of marker genes from each cluster identified in scRNAseq with hemolymph fractions enriched for different hemocyte morphotypes. This approach allowed them to correlate three of the seven cell types, namely hyalinocytes (H), small granule cells (SGC), and vesicular cells (VC). A macrophage-like (ML) cell type was correlated through the expression of macrophage-specific genes and its capacity to produce reactive oxygen species. Three other cell types correspond to blast-like cells, including an immature blast cell type from which distinct hematopoietic lineages originate to give rise to H, SGC, VC, and ML cells. Additionally, ML cells and SGCs demonstrated phagocytic properties, with SGCs also involved in metal homeostasis. On the other hand, H cells, nongranular cells, and blast cells expressed antimicrobial peptides. This study thus provides a complete landscape of oyster hemocytes with functional validation linked to immune activities. This resource will be valuable for studying the impact of bacterial or viral infections in oysters.

Strengths:

The main strength of this study lies in its comprehensive and integrative approach, combining single-cell RNA sequencing, cytological analysis, cell fractionation, and functional assays to provide a robust characterization of hemocyte populations in Crassostrea gigas.

(1) The innovative use of marker genes, quantifying their expression within specific cell fractions, allows for precise annotation of different cellular clusters, bridging the gap between morphological observations and transcriptional profiles.

(2) The study provides detailed insights into the immune functions of different hemocyte types, including the identification of professional phagocytes, ROS-producing cells, and cells expressing antimicrobial peptides.

(3) The identification and analysis of transcription factors specific to different hemocyte types and lineages offer crucial insights into cell fate determination and differentiation processes in oyster immune cells.

(4) The authors significantly advance the understanding of oyster immune cell diversity by identifying and characterizing seven distinct hemocyte transcriptomic clusters and morphotypes.

These strengths collectively make this study a significant contribution to the field of invertebrate immunology, providing a comprehensive framework for understanding oyster hemocyte diversity and function.

Weaknesses:

(1) The authors performed scRNAseq/lineage analysis and cytological analysis on oysters from two different sources. The methodology of the study raises concerns about the consistency of the sample and the variability of the results. The specific post-processing of hemocytes for scRNAseq, such as cell filtering, might also affect cell populations or gene expression profiles. It's unclear if the seven hemocyte types and their proportions were consistent across both samples. This inconsistency may affect the correlation between morphological and transcriptomic data.

We thank the reviewer for highlighting the importance of sample consistency and potential variability, and we acknowledge the need for clarification regarding the use of oysters from two different sources.

Oysters from La Tremblade (known pathogen-free in standardized conditions) were used to establish the hemocyte transcriptomic atlas through scRNA-seq and for cytological analyses. Oysters from the Thau Lagoon (Bouzigues) were used for cytological, functional, and fractionation experiments. These oysters were sampled during non-epidemic periods and monitored under Ifremer’s microbiological surveillance to ensure pathogen free status.

The cytological results (hemocytograms) presented in Figure 3 and Supplementary Figure S3 were derived from Thau Lagoon oysters. To clarify, we updated The Table 3 in Figure 3 and Supplementary Figure S3 to explicitly display hemocyte counts for oysters from both La Tremblade and Thau Lagoon. These data confirm consistent proportions of hemocyte types across both sources, with no significant differences (p > 0.05).

Hemocyte isolation and filtering protocols were rigorously optimized to preserve cell viability and morphology during scRNA-seq library preparation. Viability assays and cytological evaluations confirmed that these procedures did not significantly alter hemocyte populations or their proportions. Sample processing times were minimized to ensure that the scRNA-seq results accurately reflect the native state of the hemolymph.

Taken together, our results confirm that variability between oyster sources or methodological processes did not compromise our findings. This ensures that the correlations between morphological and transcriptomic data are reliable and robust.

(2) The authors claim to use pathogen-free adult oysters (lines 95 and 119), but no supporting data is provided. It's unclear if the oysters were tested for bacterial and viral contaminations, particularly Vibrio and OsHV-1 μVar herpesvirus.

The oysters used in this study were sourced from two distinct origins. First, the animals (18 months old) utilized for scRNA-seq and cytological analyses were obtained from the Ifremer controlled farm located in La Tremblade, France (GPS coordinates: 45.7981624714465, -1.150171788447683). This facility exclusively produces standardized oysters bred in controlled conditions with filtered seawater, entirely isolated from environmental known pathogens. The oysters from this source are certified “pathogen-free” upon arrival at the laboratory, following Ifremer's stringent quality control protocols. We have replaced the term 'pathogen-free' with 'known pathogen-free’ (line 123) to accurately reflect the animals' true status.

Second, for the fractionation experiments and functional tests, oysters were either sourced from the aforementioned Ifremer farm or from a producer located in the Thau Lagoon, France (GPS coordinates: 43.44265228308842, 3.6359883059292057). The Thau Lagoon is subject to comprehensive environmental and microbiological surveillance by the Ifremer monitoring network and the regional veterinary laboratory. For these experiments, we specifically selected oysters aged 18 months - an age associated with reduced susceptibility to OsHV-1 μVar herpesvirus - and ensured that sampling occurred outside of any detected epidemic periods. Furthermore, prior to experimentation, hemocyte samples from all oysters were examined. Oysters showing signs of contamination or exhibiting abnormal hemocyte profiles were excluded from the study.

These measures ensured that the oysters used in this work were of high health status and minimized the likelihood of bacterial or viral contamination, including Vibrio and OsHV-1 μVar.

(3) The KEGG and Gene Ontology analyses, while informative, are very descriptive and lack interpretation. The use of heatmaps with dendrograms for grouping cell clusters and GO terms is not discussed in the results, missing an opportunity to explore cell-type relationships. The changing order of cell clusters across panels B, C, and D in Figure 2 makes it challenging to correlate with panel A and to compare across different GO term categories. The dendrograms suggest proximity between certain clusters (e.g., 4 and 1) across different GO term types, implying similarity in cell processes, but this is not discussed. Grouping GO terms as in Figure 2A, rather than by dendrogram, might provide a clearer visualization of main pathways. Lastly, a more integrated discussion linking GO term and KEGG pathway analyses could offer a more comprehensive view of cell type characteristics. The presentation of scRNAseq results lacks depth in interpretation, particularly regarding the potential roles of different cell types based on their transcriptional profiles and marker genes. Additionally, some figures (2B, C, D, and 7C to H) suffer from information overload and small size, further hampering readability and interpretation.

Thank you for your valuable suggestions regarding the presentation and interpretation of our KEGG and Gene Ontology (GO) analyses. In response, we revised Figure 2 to enhance clarity and provide deeper insights into cell-type relationships and biological processes.

The revised figure 2 reorganizes GO term analysis into a more intuitive layout, grouping related biological processes and pathways in a structured manner. This approach replaces the dendrogram organization and provides a clearer visualization of key pathways for each cell cluster.

(4) The pseudotime analysis presented in the study provides modest additional information to what is already manifest from the clustering and UMAP visualization. The central and intermediate transcriptomic profile of cluster 4 relative to other clusters is apparent from the UMAP and the expression of shared marker genes across clusters (as shown in Figure 1D). The statement by the authors that 'the two types of professional phagocytes belong to the same granular cell lineage' (lines 594-596) should be formulated with more caution. While the pseudotime trajectory links macrophage-like (ML) and small granule-like (SGC) cells, this doesn't definitively establish a direct lineage relationship. Such trajectories can result from similarities in gene expression induced by factors other than lineage relationships, such as responses to environmental stimuli or cell cycle states. To conclusively establish this lineage relationship, additional experiments like cell lineage tracing would be necessary, if such tools are available for C. gigas.

We appreciate the reviewer’s detailed feedback on the pseudotime analysis and its interpretation. While we acknowledge that the clustering and UMAP visualization provide valuable insights, the pseudotime analysis offers a complementary approach by highlighting significantly expressed genes, including key transcription factors, that might otherwise be overlooked in differential expression analysis based solely on Log2FC between clusters. In our study, the pseudotime analysis revealed transcription factors known to play crucial roles in hemocyte differentiation, providing additional depth to our understanding of hemocyte lineage relationships and functional specialization.

Regarding the statement on lines 594 - 596, we agree that the evidence provided by pseudotime trajectories does not definitively establish a direct lineage relationship between macrophage-like (ML) and small granule-like (SGC) cells. Instead, these trajectories suggest potential developmental connections that warrant further investigation. We propose the following revised sentence (lines 616 to 618) :

"The pseudotime trajectory linking macrophage-like (ML) and small granule-like (SGC) cells suggests a potential developmental relationship within the granular cell lineage; however, this hypothesis requires further validation."

We also concur with the reviewer that additional experiments, such as cell lineage tracing, would be necessary to definitively establish this relationship. Unfortunately, the long-term cultivation of hemocytes in C. gigas is currently not feasible. However, we are planning to develop FACS-based approaches to separate the seven hemocyte subtypes, which will allow us to refine their ontology and explore their potential lineage relationships more precisely.

(6) Given the mention of herpesvirus as a major oyster pathogen, the lack of discussion on genes associated with antiviral immunity is a notable omission. While KEGG pathway analysis associated herpesvirus with cluster 1, the specific genes involved are not elaborated upon.

Thank you for your valuable observation regarding the lack of discussion on genes associated with antiviral immunity, particularly in the context of herpes virus infection. The KEGG pathway analysis indeed identified a weak signature associated with herpesvirus in Cluster 1, primarily involving genes encoding beta integrins. In humans, beta integrins have been described as receptors facilitating herpesvirus entry (1). However, in the case of naive oysters used in this study, the KEGG signature was subtle, likely reflecting the absence of active viral infection. Additionally, beta integrins are multifunctional molecules that also play critical roles in processes such as cell adhesion, a function attributed to hyalinocytes, as highlighted in our results.

Given the naive status of the oysters and the weak antiviral signature observed, we chose not to discuss these findings in detail in this study. However, ongoing work in our laboratory aims to further investigate the specific hemocyte populations targeted by OsHV-1, which may shed light on the role of integrins in antiviral immunity in oysters.

We hope this clarifies our approach and the context of the KEGG findings. Thank you for bringing this important perspective to our attention.

(7) The discussion misses an opportunity for comparative analysis with related species. Specifically, a comparison of gene markers and cell populations with Crassostrea hongkongensis, could highlight similarities and differences across systems.

In response to the reviewer’s comment, we have added a comparative analysis between C. hongkongensis and C. gigas hemocyte populations, situating our findings within the broader context of invertebrate immune cell diversity and specialization (lines 747 to 760)

Reviewer #2 (Recommendations for the authors):

(1) Lines 92-93: The authors should add references associated with transcriptomic studies of C. gigas hemocytes.

Thank you for pointing this out. In the revised manuscript, we have added references to previous transcriptomic studies of C. gigas hemocytes (line 83).

(2) Line 121 and 127: The authors should clarify whether 3,000 represents the number of cells loaded or their target for analysis.

The number of cells processed was optimized to minimize the occurrence of doublets during scRNAseq. Following 10x Genomics Chromium guidelines, we loaded 4,950 cells to successfully recover a target of 3,000 cells, with a doublet rate of 2.4%, well below the target threshold of 2.5%. This information has been added on line 125 of the document. The target was 3,000 cells, and as reported in Supplementary Table S1, the estimated number of cells after STAR-solo alignment was 2,937. This ensures the reliability and accuracy of single-cell transcriptomic data.

(3) Line 129: "Supp. Table 1" in the text and "Supp. Table S1" in the figure title should be edited.

The inconsistency between "Supp. Table 1" in the text and "Supp. Table S1" in the figure title has been corrected for uniformity throughout the manuscript (line 134).

(4) Line 138-139: The authors should clarify that the heatmap displays the top 10 positively enriched marker genes for each cluster, as identified by Seurat's differential expression analysis. It is important to note that the analysis does not explicitly show under-represented transcripts, but rather highlights the contrast between cluster-specific overexpressed genes and their lower expression in other clusters.

We have clarified that the heatmap displays the top 10 positively enriched marker genes for each cluster, as identified by Seurat's differential expression analysis, and that the analysis highlights cluster-specific overexpressed genes rather than explicitly showing under-represented transcripts (lines 143 - 145).

(5) Figure 1: The authors should consider improving or potentially removing Figure 1C. The gene IDs are not readable due to their small size, which significantly reduces the informative value of the figure. In addition, the data presented in this heatmap is largely redundant with the more informative and readable dot plot in Figure 1D, which shows both expression levels and the percentage of cells expressing each gene.

Thank you for your suggestion regarding Figure 1C. In the revised manuscript, we have removed the original panel C from the main figure and transferred it to Supplementary Figure S1K, which improves readability while retaining the relevant data. We have also renumbered the remaining panels for clarity, with the former panel D now designated as panel C. We believe these adjustments address the reviewer’s concerns and streamline the presentation of the data.

(6) Table 1: The authors should clarify in the legend the statistical significance criteria (adjusted p-value) for the genes listed.

As requested, we have added the adjusted p-value threshold (adj. p-value < 0.05) to the legend of Table 1.

(7) Line 188: The authors should align the text description of the KEGG pathways in cluster 7 with Figure 2A, describing Wnt signaling pathway and clarifying the terminology "endosome pathway" to ensure consistency.

In the revised text, we have aligned our description with Figure 2A by explicitly mentioning the Wnt signaling pathway in cluster 7 (lines 193 to 194).

The endo-lysosomal pathway encompasses a series of membrane-bound compartments and trafficking events responsible for the uptake of macromolecules from the extracellular environment, their subsequent sorting in endosomes, and eventual degradation in lysosomes. This pathway is tightly regulated, ensuring not only the breakdown of macromolecules but also the recycling of membrane components and signaling receptors essential for maintaining cellular homeostasis (2). In our study, the KEGG signatures of cluster 7 highlight the involvement of the endo-lysosomal pathway.

(8) Line 223: The authors should revise the description of cluster 1, avoiding references to morphology at this point in the manuscript, as no morphological data has been presented yet.

We have revised the description of Cluster 1 to remove references to morphology, ensuring consistency with the data presented at this stage of the manuscript (lines 227 to 229) : ”Cluster 1, comprising 27.6 % of cells, is characterized by GO-terms related to myosin complex, lamellipodium, membrane and actin cytoskeleton remodelling, as well as phosphotransferase activity.”

(9) Figure 2: The authors should revise Figure 2 to improve the clarity. For Figure 2A, they should address the redundancy in the "Global and overview maps" category by removing overlapping pathways such as carbon metabolism and biosynthesis of amino acids, which are likely represented in more specific metabolic categories (glycolysis, pentose). They could consider grouping similar pathways together, such as combining "Amino acid metabolism" with "Metabolism of other amino acids," and separating metabolic pathways from cellular processes for easier interpretation. They should also address the surprising absence of certain expected pathways like lipid metabolism, nucleotide metabolism, and cofactor/vitamin metabolism, as well as cellular processes such as cell growth and chromatin modeling. Even if these pathways are not enriched in specific clusters, mentioning their absence could provide valuable context for the reader.

In the revised version of the manuscript, we propose a new representation to facilitate understanding and improve the clarity of the data presentation.

(10) For Figures 2B, C, and D, the authors should significantly increase the font size of text and numbers, ensuring readability at 100% scale in PDF format. They could also add labels directly on each graph to clearly indicate the type of GO terms represented, (Biological Process, Cellular Component, or Molecular Function).

In the revised version of the manuscript, we propose a new representation to facilitate understanding and improve the clarity of the data presentation.

(11) Line 247-250: The authors should revise their description of cell types to follow the same order as presented in Figure 3A.

We have revised the description of cell types in the manuscript to follow the same order as presented in Figure 3A, as requested.

(12) Line 265-266: The authors should develop the significance of the nucleo-cytoplasmic ratio in hemocyte morphology and identification.

We thank the editor for bringing this to our attention and apologize for the discrepancy between the terminology used in the text and the results presented in Figure 3. The text refers to the nuclear-tocytoplasmic ratio (N/C), while the figure mistakenly displays the inverse ratio, cytoplasmic-to-nuclear ratio (C/N). We recognize that this inversion may cause confusion and will ensure consistency between the text and the figure.

To address this, we propose correcting the figure legend and labels in Figure 3 to align with the terminology used in the text (N/C ratio). This will prevent confusion and maintain clarity throughout the manuscript.

The nuclear-to-cytoplasmic (N:C) ratio, also known as the nucleus:cytoplasm ratio or N/C ratio, is a well-established measurement in cell biology that reflects the relative size of the nucleus to the cytoplasm. This ratio is frequently used as a morphologic feature in the diagnosis of atypia and malignancy in human cells, underscoring its diagnostic value. In the context of our study, we use the N:C ratio to provide a more precise and quantitative description of hemocyte types in Crassostrea gigas. Specifically, the N:C ratio allows us to distinguish between different hemocyte morphotypes, such as blasts and granular cells, and to enrich the characterization of their functional specialization. This quantitative measure supports the morphological classification and enhances the reproducibility and clarity of hemocyte identification.

(13) Line 286-294: The authors should review and correct the legend for Figure 3. It seems that the description of results related to Figure 3C has been mistakenly inserted into the legend.

We thank the reviewer for pointing out this issue with the legend of Figure 3. The description of results related to Figure 3C has now been removed from the legend. The revised legend focuses solely on the figure elements, improving clarity and consistency. We believe this adjustment addresses the reviewer's comment effectively.

(14) Figure 3: The authors should revise the legend for Figure 3A to provide more detailed and explicit descriptions of the "Size, shape and particularities" of the ML, SGC, BGC, and VC hemocyte types.

We thank the reviewer for their insightful suggestion to provide more explicit descriptions in the legend for Figure 3A. We have revised the legend to include detailed explanations of the "Size, shape, and particularities" for the ML, SGC, BGC, and VC hemocyte types. Specifically, we have clarified that size refers to the average granule diameter, shape describes the morphology of the granules (e.g., spherical or elongated), and particularities highlight distinguishing features such as granule color or fluorescence properties observed under specific staining or imaging conditions. We believe this updated legend provides the level of detail requested and enhances the clarity of the figure (lines 294 - 297).

(15) Figure 4: The authors should clarify the method used for calculating relative gene expression in Figure 4A and Figure 6. They should explicitly state in the figure legend that the expression was normalized to the Cg-rps6 reference gene, as mentioned in line 835. The authors should also provide details on the calculation method used (e.g., 2-ΔCt method) and confirm whether the reference gene was expressed at similar levels across all clusters.

We thank the reviewer for pointing out the need for additional clarity regarding the calculation of relative gene expression in Figures 4A and 6. To address this, we have revised the legends for both figures to explicitly state that gene expression levels were normalized to the reference gene Cg-rps6 and calculated using the 2^-ΔCt method. We have also confirmed that Cg-rps6 was stably expressed across all hemocyte clusters and explicitly mentioned this in the revised legends. These changes ensure greater transparency and address the reviewer’s concerns (lines 342 to 346).

(16) The authors could consider removing or modifying Figure 4B, as it appears to be redundant with Figure 3C. Both figures show the average percentage of each hemocyte type in the seven Percoll gradient fractions.

We thank the reviewer for highlighting potential redundancy between Figures 3C and 4B. While both figures present the distribution of hemocyte types across Percoll gradient fractions, Figure 4B serves a distinct and critical purpose in the manuscript. Specifically, it provides the numerical data necessary to understand the correlations shown in Figure 4A, where we analyze the relationship between gene expression levels and the distribution of hemocyte types. These detailed percentages are essential for interpreting the statistical robustness and biological relevance of the correlation matrix, which could not be derived solely from the qualitative visualization in Figure 3C.

(17) Figure 5: The authors should address the redundancy between Figure S7B and Figure 5B, as they appear to present the same data. In Figure S7B, "SGC" is incorrectly abbreviated as "G".

In the revised version of the manuscript, we addressed the redundancy between the two figures and we corrected the incorrectly abbreviated SGC.

(18) Line 412: The authors should correct the typographical error, changing "Pecoll" to "Percoll".

In the revised version of the manuscript, we correct this typographical error (line 417).

(19) Line 417: The statement about the inhibitor apocynin likely refers to Figure 5D, not Figure 5C.

In the revised version of the manuscript, we have corrected this reference error to accurately refer to Figure 5D (line 422).

(20) Line 441-444: The authors should provide references to support their annotation of cluster 1 as macrophage-like cells based on macrophage-specific genes. These references should cite established literature on known macrophage gene markers, particularly in bivalves or related species if available. They need to clarify whether specific gene markers exist for each of the hemocyte morphotypes they have identified. If such markers are known from previous studies, they should be mentioned and referenced.

We propose to modify lines 446 to 449 to address the reviewer's concerns. Cluster 1, which we have termed "macrophage-like" due to its pronounced phagocytic activity and reactive oxygen species (ROS) production, is enriched in Angiopoietin-1 receptor expression (Table 1). Angiopoietin receptors belong to the Tie receptor family, which is expressed in a subset of macrophages known as Tie2-expressing monocytes (TEMs) in humans (3–5). While our analysis reveals a strong overexpression of the Angiopoietin-1 receptor, we acknowledge that this receptor is not an exclusive marker for macrophages.

In bivalves, including oysters, no definitive molecular markers have been established for macrophagelike cells as they are defined functionally in this study. Consequently, the identification of such cells relies on their functional characteristics rather than strict marker expression. To clarify, we propose the following revision to the sentence:

Furthermore, this cluster expresses macrophage-related genes, including the macrophage-expressed gene 1 protein (G30226) (Supp. Data S1), along with maturation factors for dual oxidase, an enzyme involved in peroxide formation (Supp. Fig. S8), supporting its designation as macrophage-like based on functional characteristics.

(21) Figure 7: For Figures 7C to 7H, the authors should increase the font size of gene names and descriptions to ensure legibility in both printed versions and digital formats. To simplify these figures, the authors could consider displaying less differentially expressed genes for each lineage, along with the top genes for each differentiation pathway. If detailed gene information is crucial, they could move the full list to a supplementary table and reference it in the figure legend. Regarding Figure 7I, the authors should reorder the transcription factor genes by cluster and specificity to improve visualization and interpretation, like in Figure 1D.

Thank you for these valuable suggestions regarding Figure 7. We have revised Figures 7C–H to ensure improved readability. Furthermore, we have simplified these panels by highlighting fewer differentially expressed genes for each lineage. In Figure 7I, we have reordered the transcription factor genes by cluster and specificity, following a layout similar to Figure 1D, to facilitate clearer visualization and interpretation of the data.

(22) Line 490: The authors should provide more precise references to the specific GO terms and figure panels they are discussing.

To address this comment, we have revised the sentence and provided additional information in the text to clearly indicate where the corresponding figure panels can be found in the manuscript (line 499)

(23) Line 510: The authors state that "5 cell lineages could be defined," but the subsequent text and Figure 7C to H actually present 6 distinct lineages.

We have corrected in the manuscript. 6 lineages could be defined (line 521).

(24) Line 534: The authors should consider further investigating the pluripotent potential of cluster 4 cells by exploring known or potential stem cell markers in their scRNAseq data.

Thank you for highlighting the possibility of pluripotent potential of cluster 4. In our current analysis, we did not detect any known stem cell or proliferative markers, nor evidence of a clearly defined hematopoiesis site in the hemolymph. Indeed, previous work suggests that oyster hematopoiesis may occur in tissues such as the gills, implying that stem or progenitor cells might not circulate in the hemolymph under homeostatic conditions. Consequently, it is plausible that our observation of no proliferative cell populations partly reflects their absence in hemolymph, especially in naïve (unstimulated) oysters. To conclusively identify potential progenitor cells and their proliferative activity, further approaches involving deliberate perturbation of hemocyte homeostasis - such as immunological challenge (e.g., Zymosan treatment) combined with lineage-tracing or proliferation assays - would be necessary. These future investigations would not only clarify whether proliferative cells emerge in the hemolymph in response to environmental or pathological stimuli but also help elucidate the broader cellular pathways underlying oyster immune responses.

In response to the reviewer’s comment, we have revised the Discussion (lines 695 to 696) and added : “Nevertheless, we did not detect any canonical stem or progenitor cell populations in our dataset, underscoring the need for future investigations - potentially involving immunological challenges and lineage-tracing assays - to clarify whether proliferative cells circulate in the hemolymph or instead reside primarily in tissue compartments.”

(25) Figure S10: The authors should significantly improve the readability of Figure S10 by increasing the font size. Currently, the small font size makes it impossible for readers to discern the information presented.

Thank you for highlighting the readability concerns regarding Figure S10. In response to your comment, we have increased the overall size and font of the figure, ensuring that all labels and legends are clearly legible in both printed and digital formats. We believe these adjustments will allow readers to more easily interpret the information presented.

(26) Line 896: The authors should correct the typographical error on line 896 by deleting the additional bracket.

In the revised version of the manuscript, we correct this typographical error.

(27) Figure S12: The authors should address the absence of any reference to Figure S12 in the main text of the manuscript.

The reference to Supp. Figure S12 has been corrected. It was a referencing error between Supp. Figure S11(in the discussion, line 670) and Supp. Figure S12.

Bibliography:

(1) G. Campadelli-Fiume, D. Collins-McMillen, T. Gianni, A. D. Yurochko, Integrins as Herpesvirus Receptors and Mediators of the Host Signalosome. Annual Review of Virology 3, 215–236 (2016).

(2) J. P. Luzio, P. R. Pryor, N. A. Bright, Lysosomes: fusion and function. Nat Rev Mol Cell Biol 8, 622–632 (2007).

(3) A. S. Harney, E. N. Arwert, D. Entenberg, Y. Wang, P. Guo, B.-Z. Qian, M. H. Oktay, J. W. Pollard, J. G. Jones, J. S. Condeelis, Real-Time Imaging Reveals Local, Transient Vascular Permeability, and Tumor Cell Intravasation Stimulated by TIE2hi Macrophage-Derived VEGFA. Cancer Discov 5, 932–943 (2015).

(4) M. De Palma, R. Mazzieri, L. S. Politi, F. Pucci, E. Zonari, G. Sitia, S. Mazzoleni, D. Moi, M. A. Venneri, S. Indraccolo, A. Falini, L. G. Guidotti, R. Galli, L. Naldini, Tumor-targeted interferon-alpha delivery by Tie2-expressing monocytes inhibits tumor growth and metastasis. Cancer Cell 14, 299–311 (2008).

(5) M. De Palma, M. A. Venneri, R. Galli, L. Sergi Sergi, L. S. Politi, M. Sampaolesi, L. Naldini, Tie2 identifies a hematopoietic lineage of proangiogenic monocytes required for tumor vessel formation and a mesenchymal population of pericyte progenitors. Cancer Cell 8, 211–226 (2005).

Reviewer #3 (Public review):

The paper addresses pivotal questions concerning the multifaceted functions of oyster hemocytes by integrating single-cell RNA sequencing (scRNA-seq) data with analyses of cell morphology, transcriptional profiles, and immune functions. In addition to investigating granulocyte cells, the study delves into the potential roles of blast and hyalinocyte cells. A key discovery highlighted in this research is the identification of cell types engaged in antimicrobial activities, encompassing processes such as phagocytosis, intracellular copper accumulation, oxidative bursts, and antimicrobial peptide synthesis.

A particularly intriguing aspect of the study lies in the exploration of hemocyte lineages, warranting further investigation, such as employing scRNA-seq on embryos at various developmental stages.

In the opinion of this reviewer, the discussion should compare and contrast the transcriptome characteristics of hemocytes, particularly granule cells, across the three species of bivalves, aligning with the published scRNA-seq studies in this field to elucidate the uniformities and variances in bivalve hemocytes.

Reviewer #3 (Recommendations for the authors):

Minor Concerns:

(1) In the context of C. gigas, the notable expansion of stress and immune-related genes in its genome stands out. It is anticipated that the article will discuss the expression patterns of classical immune-related genes like TLR and RLR across different cell clusters.

We appreciate the reviewer's interest in the expression patterns of classical immune-related genes, such as Toll-like receptors (TLRs) and RIG-I-like receptors (RLRs), across different cell clusters in Crassostrea gigas. In our single-cell RNA sequencing (scRNA-seq) analysis, we did not detect significant expression of TLR or RLR genes. This absence can be attributed to several factors. First, technical limitations of scRNA-seq: The droplet-based scRNA-seq technology employed in our study captures only a fraction of the transcripts present in each cell approximately 10–20% (https://kb.10xgenomics.com/hc/en-us/articles/360001539051-What-fraction-of-mRNA-transcriptsare-captured-per-cell). This inherent limitation often results in the underrepresentation of genes with low expression levels. Consequently, TLRs and RLRs, which may be expressed at low levels in certain hemocytes, could be undetected due to this capture inefficiency. TLRs are typically expressed at low basal levels under resting conditions and are upregulated in response to specific stimuli or pathogenic challenges (1, 2). Given that our study analyzed hemocytes in their basal state, the expression levels of these receptors may have been below the detection threshold of the scRNA-seq platform. Furthermore, as highlighted by De Lorgeril et al. (3) the expression of these immune receptors varies depending on the resistance of the oyster. This variability further underscores the dynamic and context-dependent nature of TLR and RLR expression

To comprehensively assess the expression patterns of TLRs and RLRs across different hemocyte clusters, future studies could incorporate targeted enrichment strategies, such as bulk RNA-seq or single-cell technologies with higher capture efficiencies. Additionally, analyzing hemocytes under stimulated conditions or comparing oysters with varying levels of resistance could provide insights into the inducible and context-specific expression of these immune receptors.

(2) Clarification is needed in lines 265-266 regarding the nucleo-cytoplasmic ratio (N/C) terminology to prevent confusion, considering the discrepancy with the results presented in Figure 3.

We thank the editor for bringing this to our attention and apologize for the discrepancy between the terminology used in the text and the results presented in Figure 3. The text refers to the nuclear-tocytoplasmic ratio (N/C), while the figure mistakenly displays the inverse ratio, cytoplasmic-to-nuclear ratio (C/N). We recognize that this inversion may cause confusion and will ensure consistency between the text and the figure.

To address this, we propose correcting the figure legend and labels in Figure 3 to align with the terminology used in the text (N/C ratio). This will prevent confusion and maintain clarity throughout the manuscript.

(3) The selection of cluster 4 as the root for pseudotime analysis based on high ribosomal protein expression raises questions. It would be beneficial to elaborate on the inclusion of other genes, such as cell cycle or mitotic-related genes, to validate the pseudotime analysis outcomes.

We appreciate the reviewer’s insightful comment on the significance of ribosomal proteins in stem cell maintenance.

Hematopoietic stem cells (HSCs) are a population of stem cells that are largely cell-cycle-quiescent (G0 phase) with low biosynthetic activity. Upon stimulation and stress HScs undergo proliferation and differentiation and produce all lineages of hemocytes.

Ribosomal proteins play a multifaceted role in preserving the balance between stem cell quiescence and activation. By ensuring precise regulation of protein synthesis, they allow stem cells to maintain their undifferentiated state while remaining poised for activation when needed. Furthermore, ribosomal proteins contribute to the cellular stress response, safeguarding stem cells from oxidative damage and other stressors that could compromise their functionality. Importantly, ribosomal biogenesis and the dynamic assembly of ribosomes provide a regulatory mechanism that fine-tunes the transition from self-renewal to differentiation, a critical feature of hematopoietic stem cells (HSCs) and other stem cell types. These mechanisms collectively highlight the indispensable role of ribosomal proteins in stem cell biology, underscoring their relevance to our study's findings.

In vertebrate, the maintenance of hematopoietic stem cells (HSCs) and hematopoietic homeostasis is widely acknowledged to rely on the proper regulation of ribosome function and protein synthesis (4). This process necessitates the coordinated expression of numerous genes, including genes that encode ribosomal proteins (RP genes) and those involved in regulating ribosome biogenesis and protein translation. Disruptions or mutations in these critical genes are associated with the development of congenital disorders (5). Among these, Rpl22 (found in cluster 4 with a Log2FC of 1.59) has been shown to play a pivotal role in HSC maintenance by balancing ribosomal protein paralog activity, which is critical for the emergence and function of HSCs (6).

(4) What is the resolution of the cell clustering employed in the study? Given that cluster 1 potentially encompasses two distinct cell types, Macrophage-Like and Big Granule cells, further sub-clustering efforts and correlation analyses between cluster markers and cell morphologies could aid in their differentiation.

Thank you for your inquiry regarding the resolution of our cell clustering. As described in the Materials and Methods section, we used the Seurat FindClusters function with a resolution parameter of r = 0.1 for the scRNA-seq dataset. We performed sub-clustering within Cluster 1, resulting in four distinct subclusters. However, despite analyzing various specific markers, we did not identify any marker uniquely associated with the Big Granule Cell (BGC) morphology. Notably, LACC24 specifically marks a subset of cells within Cluster 1, as shown in Supplementary Figure S8, although this gene alone was insufficient to definitively distinguish a distinct BGC population.

(5) Line 78's statement regarding the primary identification of three hemocyte cell types in C. gigas-blast, hyalinocyte, and granulocyte cells would benefit from including references to substantiate this claim.

We thank Reviewer #1 for their valuable comments, which have allowed us to further improve our manuscript. We have enriched the introduction with the following addition (lines 79 to 82):

“Blast-like cells are considered undifferentiated hemocyte types (Donaghy et al., 2010), hyalinocytes appear to play a key role in wound repair (de la Ballina et al., 2020), and granulocytes are primarily involved in immune surveillance. Among these, granulocytes are regarded as the main immunocompetent hemocyte type (Wang et al., 2017).”

Conclusion:

The authors largely achieved their primary objective of providing a comprehensive characterization of oyster immune cells. They successfully integrated multiple approaches to identify and describe distinct hemocyte types. The correlation of these cell types with specific immune functions represents a significant advancement in understanding oyster immunity. However, certain aspects of their objectives have not been fully achieved. The lineage relationships proposed on the basis of pseudotime analysis, while interesting, require further experimental validation. The potential of antiviral defense mechanisms, an important aspect of oyster immunity, has not been discussed in depth.

This study is likely to have a significant impact on the field of invertebrate immunology, particularly in bivalve research. It provides a new standard for comprehensive immune cell characterization in invertebrates. The identification of specific markers for different hemocyte types will facilitate future research on oyster immunity. The proposed model of hemocyte lineages, while requiring further validation, offers a framework for studying hematopoiesis in bivalves.

Bibliography:

(1) J. Chen, J. Lin, F. Yu, Z. Zhong, Q. Liang, H. Pang, S. Wu, Transcriptome analysis reveals the function of TLR4-MyD88 pathway in immune response of Crassostrea hongkongensis against Vibrio Parahemolyticus. Aquaculture Reports 25, 101253 (2022).

(2) Y. Zhang, X. He, F. Yu, Z. Xiang, J. Li, K. L. Thorpe, Z. Yu, Characteristic and Functional Analysis of Toll-like Receptors (TLRs) in the lophotrocozoan, Crassostrea gigas, Reveals Ancient Origin of TLR-Mediated Innate Immunity. PLOS ONE 8, e76464 (2013).

(3) J. de Lorgeril, B. Petton, A. Lucasson, V. Perez, P.-L. Stenger, L. Dégremont, C. Montagnani, J.M. Escoubas, P. Haffner, J.-F. Allienne, M. Leroy, F. Lagarde, J. Vidal-Dupiol, Y. Gueguen, G.

Mitta, Differential basal expression of immune genes confers Crassostrea gigas resistance to Pacific oyster mortality syndrome. BMC Genomics 21, 63 (2020).

(4) R. A. J. Signer, J. A. Magee, A. Salic, S. J. Morrison, Haematopoietic stem cells require a highly regulated protein synthesis rate. Nature 509, 49–54 (2014).

(5) A. Narla, B. L. Ebert, Ribosomopathies: human disorders of ribosome dysfunction. Blood 115, 3196–3205 (2010).

(6) Y. Zhang, A.-C. E. Duc, S. Rao, X.-L. Sun, A. N. Bilbee, M. Rhodes, Q. Li, D. J. Kappes, J. Rhodes, D. L. Wiest, Control of Hematopoietic Stem Cell Emergence by Antagonistic Functions of Ribosomal Protein Paralogs. Developmental Cell 24, 411–425 (2013).

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

This paper provides a compelling analysis of chiton genomes, revealing extensive genomic rearrangements despite the group's apparent morphological stasis. By examining five reference-quality genomes, the study identifies 20 conserved molluscan linkage groups that are subject to significant rearrangements, fusions, and duplications in chitons, particularly in the basal Lepidopleurida clade. The high heterozygosity observed adds complexity to genome assembly but also highlights notable genetic diversity.

We also note the comment from this reviewer that “more information is needed to clarify how this affects genome assembly and evolutionary outcomes.” We strongly agree; although it is outside the scope of this study, this may help develop future work on that topic.

The research challenges the assumption that morphological stability implies genomic conservatism, suggesting that dynamic genome structures may play a role in species diversification. Although limited by the small number of molluscan genomes available for comparison, this study offers valuable insights into evolutionary processes and calls for further genomic exploration across molluscan clades. Some minor comments need to be tackled:

(1) Line 39: 'major changes'. Please, better explain what you mean here?

Clarified as major morphological change

(2) Lines 70-73: refer to 'extant' cephalopods.

Corrected

(3) There is an inconsistency in the use of "Callochitonida" (lines 76, 85, 140, 145, Table S3, Figure S3) and "Chitonida s.l." (Figures 2, 3, and 4) throughout the text, figures, and supplementary material. To maintain clarity and avoid confusion, I recommend choosing one taxon and using it consistently across all sections of the manuscript. This will ensure coherence and help readers follow the discussion without ambiguity.

An explanation has been added to the introduction and other instances in the text changed to Chitonida s.l. for consistency

(4) Overall, the conclusions introduce several important topics and additional information that were not addressed earlier in the paper. It would enhance the coherence and impact of the study to introduce these points in the introduction, as they highlight the broader significance and relevance of the research. Integrating these key aspects earlier on would better frame the study's objectives and provide readers with a clearer understanding of its importance from the outset.

The paragraph about chiton natural history and some additional lines have been moved to the introduction

(5) Lines 242-245 and 254-256: While I agree with the authors on the remarkable results found in molluscs, particularly in polyplacophorans, I suggest toning down the comparisons with lepidopterans. The current framing may come across as dismissive towards butterflies, which does not seem necessary. It's true that biases exist in studying taxa that are more charismatic due to factors like diversity or aesthetic appeal, but the goal should be to emphasize the value of polyplacophorans without downplaying the significance of butterfly research. Instead, the focus should be on highlighting chitons as an exciting new model for understanding key evolutionary processes like synteny, polyploidy, and genome evolution. This shift would underscore the importance of polyplacophorans in a positive light without diminishing the value of lepidopteran studies.

This sentence has been rephrased to adjust the tone of this paragraph

(6) Figure 3: should be read 'Polyplacophora'.

Corrected

Reviewer #2 (Recommendations for the authors):

I hope these comments by line number are helpful, despite my lack of experience with comparative genomics:

We note the general comment from this reviewer that “most chiton genomes seem to be relatively conserved” may be  a misunderstanding from our presentation; we have added some additional notes in the first part of the discussion to ensure that this is clear to all readers.

The reviewer also pointed out that “geologically recent events that do not especially represent the general pattern of genome evolution across this ancient molluscan taxon”. To clarify, the (limited) phylogenetic evidence suggests these changes are a longer term pattern throughout chiton evolution, since chromosomal rearrangements are found when comparing congeneric species (Acanthochitona spp., Fig 4C) and also across orders (Fig 4B). This has been added to the conclusions, as this is clearly an important point that was not adequately explained in the original text.

(1) Line 72: It is true that adaptive radiations occur and are an interesting general model for how diversification can lead to species-rich taxa. However, there are other "non-adaptive" processes that can lead to geographically isolated species that are not much differentiated in their ecological or morphological diversity. The sentence here implies that such adaptive radiation is a necessary correlation of species richness. I agree that chitons have hardly frozen in time since the Paleozoic.

This is clarified by moving some additional natural history aspects of chitons to the introduction, also as suggested by the first reviewer

(2) L113: I am curious about how this character optimization was accomplished to allow the authors to reconstruct the HAM (hypothetical ancestral mollusc) chromosome number as 20 when the range of variation in Polyplacophora is 6 to 16 (mode 11), and chitons are part of the sister taxon to conchiferans. Is this dependent on the chromosome numbers found in the outgroup?

We inferred ancestral linkage groups (“chromosomes”) based on comparison with other gastropods and bivalves noted in the methods; the other study cited (Simakov et al. 2022) used a broader selection of metazoans and also predicted an ancestral Mollusca karyotype of 1N=20.

(3) L116: "Using five chromosome-level genome assemblies for chitons, we reconstructed the ancestral karyotype for Polyplacophora (more strictly the taxonomic order Neoloricata), and all intermediate phylogenetic nodes to demonstrate the stepwise fusion and rearrangement of gene linkage groups during chiton evolution (Fig. 3)."

This is probably fine, but I had to struggle to understand what genome events happened between the Acanthochitona species. Are the chromosomes merely ordered and numbered by chromosome size and the switch in position between chromosomes 1 and 3 just has to do with the chromosomes 4+5, so they become the largest chromosome, and the former 1 is now 3? Confusing! The way it is drawn it seems like this implies more genome rearrangement than occurred, whereas if the order was maintained it would be more obvious that there were simply two chromosome fusions.

The linkage groups are numbered in order of size, which is the typical way they would each be presented if the taxon was illustrated alone. Here this allows the reader to understand how the fusions or rearrangements have shifted the volume of genetic information between groups especially in comparison to the molluscan or polyplacophoran ancestor. In Fig 4 we instead decided to present the linkage groups in a revised form, so that each transition from the nearest ancestor is visible in more detail. We have added these points in the figure caption for Fig 3 which should make it easier for new readers to understand the presentation.

(4) L481: Typo: A. rubrolineatain should be A. rubrolineata.

Corrected

(5) Figure 4: I am a little confused with what is meant by an "Ancestor" in these diagrams. For example, for comparing the two species of Acanthochitona with a hypothetical ancestor, it seems that the ancestor should be like one of the two, not different from both.

I am looking at Ancestor "3" compared with the Acanthochitona rubrolineata "3" and A. discrepans "4". Again, I assume that the latter is "4" because it is slightly smaller than a new "3" and now the new "3" corresponds to "1" in the other Acanthochitona. This figure does help interpret Figure 3.

To the point about reconstructing ancestral types; the two species both descended from a common ancestor. In morphology it is sometimes clear that one lineage retains more plesiomorphic character states; but in this case we must assume equal probability of change in any direction. The ancestor is a compromise that estimates the shortest distance to both descendants.

We understand how the numbers were unclear and potentially distracting. This has been added to the figure caption, we are grateful for the feedback that will certainly help future readers.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study investigates protein-protein interactions (PPIs) within the nuage, a germline-specific organelle essential for piRNA biogenesis in Drosophila melanogaster, using AlphaFold2 to predict interactions among 20 nuage-localizing proteins. The authors identify five novel interaction candidates and experimentally validate three of them, including Spindle-E and Squash, through co-immunoprecipitation assays. They confirm the functional significance of these interactions by disrupting salt bridges at the Spn-E_Squ interface. The study further expands its scope to analyze approximately 430 oogenesis-related proteins, validating three additional interaction pairs. A comprehensive screen of around 12,000 Drosophila proteins for interactions with the key piRNA pathway player, Piwi, identifies 164 potential binding partners. Overall, the research demonstrates that in silico approaches using AlphaFold2 can link bioinformatics predictions with experimental validation, streamlining the identification of novel protein interactions and reducing the reliance on extensive experimental efforts. The manuscript is commendably clear and easy to follow; however, areas for improvement should be addressed to enhance its clarity and rigor.

Major Concerns:

(1) While AlphaFold2 was developed and trained primarily for predicting protein structures and their interactions, applying it to predict protein-protein interactions is an extrapolation of its intended use. This introduces several important considerations and risks. First, it assumes that AlphaFold's accuracy in structure prediction extends to interactions, despite not being explicitly trained for this task. Additionally, the assumption that high-scoring models with structural complementarity imply biologically relevant interactions is not always valid. Experimental validation is essential to address these uncertainties, as over-reliance on computational predictions without such validation can lead to false positives and inaccurate conclusions. The authors should expand on the assumptions, limitations, and risks associated with using AlphaFold2 for predicting protein-protein interactions.

We appreciate the reviewer's point. The prediction of protein-protein interactions using AlphaFold2 relies on the number of conserved homologous sequences and previous conformational data(8) (Jumper, J. et al. Highly accurate protein structure prediction with AlphaFold. Nature 596, 583–589 (2021)). We added sentences explaining the limitations and risks of the AlphaFold2 prediction method in Introduction and the end of Result and Discussion of the revised manuscript, respectively.

Page 5, Line 67;

“AlphaFold2 requires sequence homology information to predict protein-protein interactions and the complex structure model. The reliability of these predictions is basically dependent on the strength of co-evolutionary signals(9).”

Page 6, Line 84;

“AlphaFold2 was initially trained to predict the structure of individual proteins(8). Its application to complex prediction is an extrapolative use beyond its original intended scope, and its accuracy remains unverified. Even high-confidence predictions may not correspond to actual interactions, necessitating experimental validation to confirm whether predicted protein dimers truly bind.”

Page 21, Line 361;

“This study identifies several potential protein interactions, but AlphaFold2 predictions require caution. Protein-protein interactions involve conformational changes and dependencies on ligands, ions, and cofactors, which AlphaFold2 does not consider, potentially reducing prediction accuracy. Notably, the presence of a high-scoring model in terms of structural complementarity does not guarantee that the interaction is biologically significant.”

(2) The authors experimentally validated three interactions, out of five predicted interactions, using co-immunoprecipitation (co-IP). They attributed the lack of validation for the other two predictions to the limitations of the co-IP method. However, further clarification on the potential limitations of the co-immunoprecipitation behind the negative results would strengthen the conclusions. While co-IP is a widely used technique, it may not detect weak or transient interactions, which could explain the failure to validate some predictions. Suggesting alternative validation methods such as FRET or mass spectrometry could further substantiate the results. On the other hand, AlphaFold2 predictions are not infallible and may generate false positives, particularly when dealing with structurally plausible but biologically irrelevant interactions. By acknowledging both the potential limitations of co-IP and the possibility of false positives from AlphaFold2, the authors can provide a more balanced interpretation of their findings.

We appreciate the reviewer's point of view. We have used the co-IP method to detect interactions in this study. However, as the reviewer pointed out, it is likely that weak and transient interactions may not be detected. We added a note on the detection limits of the co-IP method and the possibility that AlphaFold2 method produces false positives in the revised manuscript.

Page 12, Line 197;

“While co-immunoprecipitation is a widely used method, it may not always detect weak or transient interactions. Other validation methods, such as FRET or co-localization assay in culture cells, could offer further insights to support the results. It is also important to note that AlphaFold2's predictions are not definitive and may lead to false positives, particularly when analyzing a large number of interactions.”

(3) In line 143, the authors state that "This approach identified 13 pairs; seven of these were already known to form complexes, confirming the effectiveness of AlphaFold2 in predicting complex formations (Table 2). The highest pcScore pair was the Zuc homodimer, possibly because AlphaFold2 had learned from Zuc homodimer's crystal structure registered in the database." While the authors mentioned the presence of the Zuc homodimer's crystal structure, they do not provide a systematic bioinformatics analysis to evaluate pairwise sequence identity or check for the presence of existing structures for all the proteins or protein pairs (or their homologs) in databases such as the Protein Data Bank (PDB) or Swiss-Model. Conducting such an analysis is critical, as it significantly impacts the novelty and reliability of AlphaFold2 predictions. For instance, high sequence identity between the query proteins could lead to high-scoring models for biologically irrelevant interactions. Including this information would strengthen the conclusions regarding the accuracy and utility of the predictions.

We appreciate the reviewer's critical point. The AlphaFold2 method generates a high confidence score when the 3D structure of the protein of interest, or of proteins with very similar sequences, is solved. We investigated whether the proteins used in this study are included in the 3D structure database (PDB) and added the information as a supplemental table S2. The following sentences were added to explain the structural references that AlphaFold2 has learned in the revised manuscript.

Page 9, Line 150;

The structures of the 20 proteins used in this study have been analyzed to varying extents in previous studies (Supplementary Table S2). A complex of Vas and the Lotus domain of Osk has been reported(20), and based on this complex structure, the interaction between Vas and Tej Lotus domain was predicted with a high score. Although the conformational analyses of the RNA helicase domain and the eTud domain have been reported previously, many of those cover only a subset of the regions and unlikely to affect our predictions in this study.

The predicted 3D structures and the Predicted Aligned Error (PAE) plots for the 12 pairs, are shown in Fig. 1C.

(4) While the manuscript successfully identifies novel protein interactions, the broader biological significance of these interactions remains underexplored. The manuscript could benefit from elaborating on how these findings may contribute to understanding the piRNA pathway and its implications on germline development, transposon repression, and oogenesis.

We added to the revise manuscript the potential biological significance of the novel protein-protein interactions presented in this manuscript as follows;

Page 16, Line 268;

“In this study, three novel protein-protein interactions were predicted and experimentally confirmed. AlphaFold2 also predicted the 3D structure of these complexes, providing insight into the important regions involved in complex formation. These predictions will provide fundamental information to elucidate nuage assembly. Nuage is thought to form by liquid-phase separation; however, direct protein-protein interactions likely occur within protein-dense nuage, facilitating RNA processing. Although the precise roles of individual interactions require further study, characterization of protein-protein interactions within nuage will help clarify the mechanism of piRNA production.”

Reviewer #1 (Recommendations for the authors):

Minor Concerns:

(1) In the Materials and Methods section, the authors thoroughly describe the computational infrastructure (SQUID at Osaka University) and the use of AlphaFold2. However, it would greatly benefit the readers to include a detailed breakdown of the computational cost. Understanding the computational cost (in terms of time, CPU/GPU hours, or other relevant metrics) for predicting 3D structures, especially for 400 protein pairs, would provide valuable insight into the efficiency and scalability of the approach. This would enhance the practical relevance of the methodology section and offer a better understanding of the resources required, beyond just the infrastructure description.

Thank you for your valuable suggestion. The following descriptions were added in the revised manuscript.

Page 24, Line 403;

“The calculation of the MSA took on average 2-4 hours per protein, with the more homologs of the protein in query, the longer it took.”

Page 24, Line 409;

“Prediction of dimer structure took approximately 1-2 hours per pair on average, depending on protein size. Each user can compute 100~200 pairs of calculations per day, but since the supercomputer is shared, job availability varies with overall demand.”

(2) The manuscript will benefit from a review for grammatical accuracy and clarity, especially in complex explanations. For example, in Line 160: "The predicted dimer structures of Me31B_Tral and Cup_Me31B showed the score of 0.74 and 0.68, respectively (Table 2)." could be revised to "The predicted dimer structures of Me31B_Tral and Cup_Me31B showed scores of 0.74 and 0.68, respectively.

Thank you very much for pointing it out. Correction has been made to the text pointed out (Page 10, Line 170).

(3) For alphafold3 webserver, please use (https://alphafoldserver.com/) instead of (https://golgi.sandbox.google.com/about).

Thank you very much for pointing it out. The URL has been changed in the revised manuscript (Page 25, Line 422).

Reviewer #2 (Public review):

Summary:

In this paper, the authors use AlphaFold2 to identify potential binding partners of nuage localizing proteins.

Strengths:

The main strength of the paper is that the authors experimentally verify a subset of the predicted interactions.

Many studies have been performed to predict protein-protein interactions in various subsets of proteins. The interesting story here is that the authors (i) focus on an organelle that contains quite some intrinsically disordered proteins and (ii) experimentally verify some (but not all) predictions.

Weaknesses:

Identification of pairwise interactions is only a first step towards understanding complex interactions. It is pretty clear from the predictions that some (but certainly not all) of the pairs could be used to build larger complexes. AlphaFold easily handles proteins up to 4-5000 residues, so this should be possible. I suggest that the authors do this to provide more biological insights.

We thank the reviewer for his kind suggestions. In this study, protein dimers were screened on the assumption that the two proteins bind 1:1; in some cases, multiple binding partners were predicted for a single protein. For example, Spn-E was predicted to bind Tej and Squ, respectively. Therefore, for Spn-E_Squ_Tej, we used the latest AlphaFold3 to predict the trimeric structure, which has already been described in the first manuscript. In addition, as suggested by the reviewer, other possible trimer results were also added in the revised manuscript as follows;

Page 15, Line 249;

“In addition to the Spn-E_Squ_Tej complex, 1:1 dimer prediction described above further suggested potential trimers (Fig. 1; Supplemental Fig. S4). For example, Tej protein is predicted to bind both Vas and Spn-E, and AlfaFold3 indeed further predicted a Vas_Tej_Spn-E trimer, where Tej’s Lotus and eTud domains interact with Vas and Spn-E, respectively. However, Lin et al. reported that Tej binds exclusively either with Vas or Spn-E, but not simultaneously(17), in Drosophila ovary, suggesting that the predicted trimers may be weak or transient. Similarly, the BoYb_Vret_Shu and the Me31B_Cup_Tral trimers remain hypothetical and require experimental verification (Supplemental Fig. S4).”

Another weakness is the use of a non-standard name for "ranking confidence" - the author calls it the pcScore - while the name used in AlphaFold (and many other publications) is ranking confidence.

“pcScore” has been changed to “ranking confidence”

Reviewer #2 (Recommendations for the authors):

(1) The pcScore is actually what is called RankingConfidence. Also, many other measures have been developed by other groups (based on PAE for instance) - these could be compared.

Thank you for your valuable suggestions. While other indicators are being developed, we have computed the affinity of the complex based on the predicted three-dimensional structure by using PRODIGY web server. The description was added in the revised manuscript as follows;

Page 18, Line 300;

“The ranking confidence score reflects the reliability of AlphaFold2's predicted structure but does not always ensure accuracy. Therefore, we assessed complex affinity based on the predicted three-dimensional structures (Supplemental Table S6). Most dimers with high ranking confidence scores exhibited low Kd values indicative of high affinity, while some showed high Kd values indicating weak interactions (Supplemental Table S6). For example, the Baf_Vas complex had a high AlphaFold2 ranking confidence score (0.85) but a relatively high Kd value (1.1E-4 M), indicating low affinity. Consistently, Baf_Vas binding was not detected in Co-IP experiments (Fig. S5C). Although accurate Kd prediction may be limited due to insufficient structural optimization, it could serve as a valuable secondary screening tool following AlphaFold2 predictions.”

(2) A statistical estimate of FDR for binding to the PIWI protein needs to be estimated. It is possible that 1.6% of random proteins (from another species for instance) also obtain ranking confidence over 0.6, i.e. how trustful are the predictions?

Thank you for the insightful comments. Unfortunately, it is difficult to infer the FDR from the value of ranking confidence. Presumably, the accuracy will vary depending on the target protein, since the number of homologs and known conformational information will differ. In the case of Piwi, the FDR is expected to be relatively low since the conformation of the protein on its own has been experimentally determined. However, even for Piwi complexes with high values of ranking confidence, the estimated affinity varied from high to low (Supplemental Table S6). Therefore, it may be useful to conduct further secondary evaluation for AlphaFold2 predictions with high ranking confidence.

(3) Identification of pairwise interactions is only a first step towards understanding complex interactions. It is pretty clear from the predictions that some (but certainly not all) of the pairs could be used to build larger complexes. AlphaFold easily handles proteins up to 4-5000 residues, so this should be possible. I suggest that the authors do this to provide more biological insights.

Already mentioned above.

(4) The comparisons of ranking confidence vs ipTM/pTM are less interesting (by definition ranking confidence is virtually identical to ipTM).

Thank you for the thoughtful comment. As the reviewer pointed out, there is not much difference between ranking confidence and ipTM shown in Fig. 1A. A high value of pTM (firmly folding) tends to increase ranking confidence, while a low value of pTM (many disorder regions) tends to decrease ranking confidence. Therefore, it may be useful to change the threshold for confidence for each protein pair.

Author response:

We thank the reviewers for the detailed evaluations and thoughtful comments, which have improved the clarity and readability of this manuscript. We have responded to all reviewer comments and incorporated their suggested changes into the text and figures. We have also included new experimental results suggested by reviewer 2, which further strengthen our main conclusion.

Point-by-point description of the revisions

Reviewer #1:

(1) Introduction, page 3: The statement "Single dimeric kinesin moves processively along microtubules in a hand-over-hand manner by alternately moving the two heads in an 8-nm step toward the plus-end of the microtubule" is inaccurate. The kinesin heads take ~16 nm steps, while the center of mass advances in ~8 nm increments. Please adjust the wording accordingly.

(2) Introduction, page 5: In the sentence "These results are consistent with the closed and open conformations of the nucleotide-binding pocket in the rear and front heads of microtubule-bound kinesin dimers observed in cryo-electron microscopy (cryo-EM) studies," I recommend changing the order to align with the previous sentence. The correct order would be "These results are consistent with the open and closed conformations of the nucleotide-binding pocket in the front and rear heads."

We thank the reviewer for pointing out our misunderstandings. We have corrected these sentences accordingly (lines 45-47 and lines 111-112).

Reviewer #2:

MAJOR CONCERNS

Limitations of this study: The authors need to discuss the limitations of their work. 1) They used a cys-lite kinesins mutant and introduced new surface-exposed cysteines. These mutants have lower kcat values than WT. 2) They used fluorescently labeled ATP molecules, which are hydrolyzed 10 times slower than unlabeled nucleotides. 3) They still observe crosslinking under reducing conditions and partial (but almost complete) crosslinking under oxidized conditions. 4)They assumed that cysteine crosslinked orientation mimics the orientation of the neck-linker in the front and rear conditions. The authors clearly pointed to these issues in the Results section. While these assumptions are also supported by several control experiments, the authors need to acknowledge some of these limitations in the Discussion as well.

We have now reiterated some of the key caveats in the Discussion, and newly described in the Results section those points not mentioned in the original manuscript that do not affect the conclusion. We also added a summary of the limitations and caveats into the first paragraph of the Discussion section (lines 425-431).

(1) We added a sentence in the Results section to describe that the ATP-binding kinetics of the Cys-light mutant remained consistent with previous studies as follows: “First, we demonstrated that k₊₁ and k_-1 of the wild-type head without Cys-modification were unchanged after oxidization (Table 1) and were comparable to those previously reported (Cross, 2004)” (lines 163-166). The reduced kcat values of cysteine pair-added mutants before crosslinking were primarily due to reduced microtubule association rate (data not included in this manuscript). We have added a sentence in the Results section describing the kcat results as follows: “The reduced ATPase activity primarily results from a decreased microtubule association rate (data to be presented elsewhere) with little change in ATP binding or microtubule dissociation rates (Table 1).” (lines 144-146).

(2) Fluorescently-labeled ATP was used to determine the ATP off-rates of the E236A mutant monomer and E236A rear head of the E236A/WT heterodimer. Two caveats in these measurements could lead to underestimating the ATP off-rate: 1) The off rate of Alexa-ATP from the head may be reduced compared to unmodified ATP, as Alexa-ATP driven motility showed a 10-fold reduce velocity. 2) The ATP off-rate of the E236A mutant may differ from that of the rear head in the wild-type dimer, since the E236A mutant likely stabilizes the neck linker-docked state more strongly than in the rear head of the wild-type dimer. These points are crucial for evaluating the results of ATP off-rate and the affinity for ATP, so we have added sentences in the Discussion section as follows: “We note, however, that this K_d of ATP may somewhat underestimate the true value in wild-type kinesin for two reasons: first, the E236A mutation likely stabilizes the neck linker-docked, closed state more than in the rear head of the wild-type dimer (Rice et al., 1999), and second, the Alexa-ATP used to measure the ATP off-rate of E236A head showed ~10-fold smaller velocity compared to unmodified ATP, partly due to a slower ATP off-rate (Figure 2-figure supplement 3).” (lines 449-454).

(3) Under reducing condition, the rear head crosslink contained 30% crosslinked species, while under oxidized condition, the front head crosslink contained 11% un-crosslinked species (Figure 1-figure supplement 1). These heterogeneities likely affect the rate constants of K_-1 for rear head crosslink and K₂ for front head crosslink, as crosslinked and un-crosslinked species showed significantly different rate constants. However, we did not use the rear head crosslink result to determine K_-1, since ATP hydrolysis likely occurred before reversible ATP dissociation. Instead, we used E236A monomer to estimate the K_-1 of the rear head. In addition, the result for K₂ of the front head crosslink was further validated using the E236A/WT heterodimer, which will be described in the next section.

(4) This is an important point, and therefore, we conducted experiments using the E236A/WT heterodimer (including new experimental results of ATP binding kinetics of the front head) and obtained consistent results. To address this point, we have revised the following sentences in the Discussion: “In the front head, backward orientation of the neck linker has little effect on ATP binding and dissociation rates, both when measured for a monomer crosslink (Figure 2A, B) and for the front head of a E236A-WT heterodimer (Figure 4B, C, F).” (lines 432-433); “However, we found that the ATP-induced detachment rates from microtubule (K₂) were similarly reduced for both the front head crosslink (7.0 s^-1; Figure 3A) and the front WT head of the E236A/WT heterodimer (6.3 s^-1; Figures 6D), suggesting that a step subsequent to ATP binding is gated in the front head.” (lines 437-441).

Line 238, the authors wrote that "forward constraint on the neck linker in the rear head does not significantly accelerate the detachment from the microtubule." Can the authors comment on why the read-head-like construct has a low affinity for microtubules even in the absence of ATP (Line 220)? I believe that the low affinity of the head in this conformation is more striking (and potentially more important) than the changes they observe in detachment rates. The authors should also consider that they might not be able to reliably measure the changes in the dissociation rate in single molecule assays of this construct (especially if the release rate of the rear head in the oxidized condition increases a lot higher than that of WT). The kymographs show infrequent and brief events, which raises doubts about how reliably they can measure the release rates under those imaging conditions. Higher motor concentrations and faster imaging rates may address this concern.

The low microtubule affinity of the rear-head-like crosslink stems from an extremely slow ADP release rate upon microtubule binding, not from a fast microtubule-detachment rate. Using stopped-flow measurements of microtubule-binding kinetics (microtubule-stimulated mant-ADP release and microtubule association rates), we found that the rear-head-crosslink resulted in a 2,000-fold decrease in the microtubule-stimulated ADP-release rate. This finding also explains the reduced ATPase of the rear-head-crosslink (Figure 1E). Since this low microtubule-affinity state occurs in the ADP-bound state rather than the ATP-bound state, we hypothesized that the neck-linker docked ADP-bound state cannot effectively bind to microtubules, requiring neck-linker undocking for microtubule binding (Mattson-Hoss et al., Proc. Natl. Acad. Sci., 111, 7000-7005 (2014)). While we acknowledge that understanding slow microtubule binding in the neck linker docked state is important for elucidating the mechanism and regulation of microtubule-binding of the head, this paper focuses specifically on the mechanism and regulation of “microtubule-detachment”. We plan to present these microtubule-binding kinetics data in a separate manuscript currently in preparation.

To explain the low microtubule affinity of the rear-head-crosslink, we added this explanation to the text; “because this constraint on the neck linker dramatically reduces the microtubule-activated ADP release rate (data to be presented elsewhere), creating a weak microtubule binding state” (lines 226-228).

Although the rear head crosslinking construct under oxidative condition showed fewer fluorescent spots per kymographs (images) due to its low microtubule binding rate, we collected more than one hundred spots by recording additional microscope movies (N=140; Figure 3-figure supplement 2B), ensuring sufficient data for statistical analysis.

Figure 2: How do the rates shown in Figure 2A-B compare to the previous kinetics studies in the field? The authors compare the dissociation rate of WT measured in rapid mixing experiments to that of E236A in smFRET assays. It is not clear whether these comparisons can be made reliably using different assays. Can the authors perform rapid mixing of E236A or try to determine the rate for the WT from smFRET trajectories?

The results of ATP on/off rates are comparable to the previous stopped flow measurements of ATP binding to monomeric kinesin-1 on microtubule, which are 2-5 µM^-1s^-1 and ~150 s^-1, respectively (summarized in the review by Cross (2004)). We added a sentence as follows: “First, we demonstrated that K₊₁ and K_-1 of the wild-type head without Cys-modification were unchanged after oxidization (Table 1) and were comparable to those previously reported (Cross, 2004).” (lines 163-166).

As the reviewer pointed out, the rapid mixing and smFRET data cannot be directly compared due to the differences in temporal resolution and fluorescent probe used. In Figure 2E (2F in the revised version), we measured ATP dissociation rate for both WT and E236A using smFRET. Due to the lower temporal resolution, we could not accurately determine ATP binding rate using smFRET. Therefore, to compare the ATP binding rate between WT and E236A heads, we now have added stopped-flow measurements of mant-ATP binding to the E236A monomer, as shown in Fig. 2C and Figure 2-supplement 2, and described in the text (lines 182-185).

Line 396: One of the most significant conclusions of this work is that the backward orientation of the neck linker has little effect on ATP binding to the front head. This is only supported by the results shown in Fig. 2A-B. Can the authors perform/analyze smFRET assays on the E236A/WT heterodimer to directly show whether the ATP binding rate to the WT head is affected or not affected by the orientation of the neck linker of the WT head?

We agree with the reviewer that our finding about ATP binding to the front head is potentially significant in the kinesin field, as it has been widely believed that ATP-binding is suppressed in the front head. In our original manuscript, this conclusion was supported only by the measurement of ATP on-rate of the front-head-crosslink, which may differ from the front head of a dimer in which the backward orientation of the neck linker is maintained by the backward strain. Although the reviewer suggested performing smFRET experiments using E236A/WT heterodimer, smFRET have relatively low temporal resolution (50-100 fps) and cannot accurately measure the frequency of ATP binding, so we used this technique only to determine ATP off rates. In this revised manuscript, we now have added stopped-flow experiments to separately measure the ATP binding to the front and rear heads of the E236A/WT heterodimer. By labeling the rear E236A head with a fluorophore to quench the mant-ATP signal bound to the rear head, we successfully measured mant-ATP binding rate to the front head. We found that the ATP-binding rate to the front head was comparable to that of an unconstrained monomer head, providing direct evidence for our conclusion. The revised version includes Fig. 4 A-C (with Figure 4-supplement 2; Figs. 4 and 5 are swapped in order) showing the kinetics of ATP binding to the front and rear heads of the E236A/WT heterodimer, with corresponding text in the result section (lines 315-324).

MINOR CONCERNS

Lines 31 and 32: I recommend replacing "ATP affinity" with "ATP binding rate" or "the dissociation of ATP" to be more specific. This is because they do not directly measure the affinity (Kd), but instead measure the on or off rates.

Line 41: Replace "cellar" with "cellular".

Line 83: The authors should cite Andreasson et al. here.

We have corrected these sentences accordingly (lines 31, 40, 85).

Lines 83-86: It seems this sentence belongs to the next paragraph. It also needs a citation(s).

This statement lacks experimental evidence and may confuse readers, so we have removed it for clarity.

Line 151: It would be helpful to add a conclusion sentence at the end of this paragraph to explain what these results mean to the reader.

A conclusion sentence of this paragraph has been added: “These results demonstrate that neck linker constraints in both forward and rearward orientations inhibit specific steps in the mechanochemical cycle of the head (lines 151-153)”.

Lines 175-180: I recommend combining and shortening these sentences, as follows, to avoid confusing the reader: "To detect the ATP dissociation event of the rear head, we employed a mutant kinesin with a point mutation of E236A in the switch II loop, which almost abolishes ATPase hydrolysis and traps in the microtubule-bound, neck-linker docked state,"

We have corrected these sentences accordingly (line 179-181).

Line 314: "which was rarely observed ...". This is out of place and confusing as is. I recommend moving this sentence after the sentence that ends in Line 295.

This sentence explains how the dark-field microscopy data was analyzed to determine whether the labeled head was in the leading or trailing position before detaching from the microtubule, but the explanation needs clarification. We removed the phrase “which was rarely observed for E236A-WT heterodimer” and simplified this sentence as follows: “Moreover, these observations allow us to distinguish whether the gold-labeled WT head was in the leading or trailing position just before microtubule detachment; the backward displacement of the detached head indicates that the labeled WT head occupied the leading position prior to detachment (Figure 5-figure supplement 1).” (lines 347-351).

Line 300: Can the authors comment on why E236A/WT has a substantially lower ATPase rate than WT homodimer? Is it possible to determine which step in the catalytic cycle is inhibited?

We demonstrated that the k₂ (microtubule-detachment rate) of the front head matched the ATP turnover rate of the E236A/WT heterodimer (Figure 6 B and E), suggesting that the inhibited step occurs after ATP binding in the front head. In contrast, the rear E236A head showed virtually no ATP hydrolysis activity, since in high-speed dark field microscopy, we observed forward step caused by rear E236A head detachment from microtubule only rarely, approximately once every few seconds (Figure 5-figure supplement 1). We added a sentence in the text as follows: “As described later, the reduced ATPase rate results from suppressed microtubule detachment of the front WT head, while the rear E236A head is virtually unable to detach from microtubules” (lines 311-313).

Line 323: Is the unbound dwell time unchanged?

The unbound dwell time exhibited a weak ATP-dependence, which we described only in Figure 5-supplement 2 (Figure 4-supplement 2 in the old version). We observed three distinct phases in the unbound dwell time based on mobility differences, with ATP dependence appearing only in the third phase. This finding suggests that ATP binding to the microtubule-bound E236A head is sometimes necessary for the detached WT head to rebind to the forward-tubulin binding site, indicating that the microtubule-bound E236A head occasionally releases ATP during the one-head-bound state (without the forward neck linker strain). To describe the ATP-dependence of the unbound dwell time, we added a sentence in the main text as follows: “In contrast, the dwell time of the unbound state of the gold-labeled WT head showed weak ATP dependence (Figure 5-figure supplement 2), indicating that the rear E236A head occasionally releases ATP when the front head detaches from the microtubule and the neck linker of E236A head becomes unconstrainted. This finding further supports the idea that forward neck linker strain plays a crucial role in reducing the reversible ATP release rate.” (lines 372-377).

Line 331: I recommend replacing "ATP-induced detachment" with "nucleotide-induced detachment" for clarity.

We have revised the phrase accordingly (line 371).

Line 344: I recommend replacing "affinity" with "forward strain prevents the release of the nucleotide" or similar to avoid confusion. Forward strain reduces the off-rate of the bound nucleotide, rather than allowing ATP to bind more efficiently to the rear head.

We agree to the reviewer’s comment and have corrected this sentence accordingly (line 338).

Lines 376-385: G7-12 constructs are introduced in Figure 6, but the results in this paragraph are shown in Figure 5. They should be moved to Figure 6 to avoid confusion.

To improve the readability, we have reorganized Figures 4-6, such that all the figure panels related to the neck linker extended mutants are shown in Figure 6; Figure 5D has been moved to Figure 6F.

Line 421: delete "not" before "does not".

We have corrected this typo.

Lines 433-441: Unless I am mistaken, more recent work in the kinesin field showed that backward trajectories of kinesin 1 reported by Carter and Cross are due to slips from the microtubule rather than backward processive runs of the motor.

The slip motion demonstrated by Sudhakar et al. (2021) differs from the backstep motion reported by Carter and Cross (and many other laboratories). Slip motion occurs after kinesin detaches from the microtubule and continues until the bead returns to the trap center. In contrast, backstep motion occurs during processive movement when the trap force either exceeds or approaches the stall force. The kinetics of these motions also differ significantly: slip steps occur with a dwell time of 71 µs and are independent of ATP concentration, while backsteps take ~0.3 s (at 1 mM ATP) and depend on ATP concentration. These differences indicate that slip motion is phenomenologically distinct from backsteps occurring under supra-stall or near-stall force.

Line 474: Replace "suppresses" with "suppressed".

We have corrected this typo.

Figure 4E: I would plot these results with increasing ATP concentration on the x-axis.

We formatted Figure 4E to match Figure 4b from Isojima et al. (Nature Chem. Biol. 2015), to emphasize the difference in ATP dependence of the front and rear head.

Figure 4B: The authors should explain how they distinguish between bound and unbound states in the main text or figure legends. For example, it is not clear how the authors score when the motor rebinds to the microtubule in the first unbinding event shown in Figure 4B (displacement plot).

The method was described in the Materials and Methods section, but we have now described how to distinguish between bound and unbound states in the main text as follows: “Unlike the unbound trailing head of wild-type dimer that showed continuous mobility (Isojima et al., 2016), the unbound WT head of E236A-WT heterodimer exhibited a low-fluctuation state in the middle (Figure 5B, s.d. trace). This low-fluctuation unbound state was distinguishable from the typical microtubule-bound state, having a shorter dwell time of ~5 ms compared to the bound state and positioning backward, closer to the E236A head, relative to the bound state (Figure 5-figure supplement 2).” (lines 351-356).

Reviewer #3:

Minor Issues:

- Line 22, Abstract - The phrase "move in a hand-over-hand manner" could be clearer if phrased as "move in a hand-over-hand fashion" to improve readability.

We changed the word “manner” to “process” (line 23).

- Abstract - Neck linker conformation in the leading head: The sentence "We demonstrate that the neck linker conformation in the leading kinesin head increases microtubule affinity without altering ATP affinity" would benefit from defining this conformation as "backward" for clarity.

- Abstract - Neck linker conformation in the trailing head: The sentence "The neck linker conformation in the trailing kinesin head increases ATP affinity by several thousand-fold compared to the leading head, with minimal impact on microtubule affinity" should also clarify that this conformation is "forward."

We have corrected these sentences accordingly (line 30, 32).

- Abstract - Conformation-specific effects: The authors mention conformation-specific effects in the neck linker structure but do not define the neck linker's conformation or the motor domain's (MD) conformation. Clarifying these conformational changes would improve the explanation of how they promote ATP hydrolysis and dissociation of the trailing head before the leading head detaches from the microtubule, thereby providing a kinetic basis for kinesin's coordinated walking mechanism.

We have revised the last sentence of the abstract accordingly by specifying the neck linker’s conformation as follows: “In combination, these conformation-specific effects of the neck linker favor ATP hydrolysis and dissociation of the rear head prior to microtubule detachment of the front head, thereby providing a kinetic explanation for the coordinated walking mechanism of dimeric kinesin.” (lines 34-37).

- Line 306 - Use of ATP in the E236A-WT heterodimer: In discussing the "ATP-induced detachment rate of the WT head in the E236A-WT heterodimer," the authors should consider justifying their choice of ATP over ADP for inducing microtubule (MT) dissociation. Since ATP typically promotes tighter MT binding and ATP turnover is reduced in forward-positioned WT heads, it may be unclear to some readers why ATP was chosen.

We measured the ATP-induced detachment rate k₂ of the front head of the E236A-WT heterodimer to validate our findings from the front-head-crosslinked monomer experiments, which demonstrated reduced k₂ after oxidation. To clarify this point, we have now included ATP binding kinetics measurements for both front and rear heads of the E236A-WT heterodimer, as suggested by reviewer 2. These additional data demonstrate consistency between the results from the crosslinked monomer and E236A-WT heterodimer experiments.

- Discussion - Backward-oriented neck linker in the front head: The discussion mentions that the backward-oriented neck linker in the front head reduces its ATP-induced detachment rate, suggesting that a step after ATP binding (e.g., isomerization, ATP hydrolysis, or phosphate release) is gated in the front head. However, the authors do not clarify that the backward neck linker orientation would imply the nucleotide pocket should be open or at least not fully closed, thus inhibiting ATP turnover. This is important because, as demonstrated in other studies, full closure of the nucleotide pocket is linked to neck linker docking. This point should be addressed earlier in the discussion.

We have addressed this point by revising this sentence as follows: “These results are consistent with an inability of the front head to fully close its nucleotide pocket to promote ATP hydrolysis and Pi release (Benoit et al., 2023), as will be discussed later.” (lines 441-443)

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review):

Summary:

Cell metabolism exhibits a well-known behavior in fast-growing cells, which employ seemingly wasteful fermentation to generate energy even in the presence of sufficient environmental oxygen. This phenomenon is known as Overflow Metabolism or the Warburg effect in cancer. It is present in a wide range of organisms, from bacteria and fungi to mammalian cells.

In this work, starting with a metabolic network for Escherichia coli based on sets of carbon sources, and using a corresponding coarse-grained model, the author applies some well-based approximations from the literature and algebraic manipulations. These are used to successfully explain the origins of Overflow Metabolism, both qualitatively and quantitatively, by comparing the results with E. coli experimental data.

By modeling the proteome energy efficiencies for respiration and fermentation, the study shows that these parameters are dependent on the carbon source quality constants K_i (p.115 and 116). It is demonstrated that as the environment becomes richer, the optimal solution for proteome energy efficiency shifts from respiration to fermentation. This shift occurs at a critical parameter value K_A(C).

This counter intuitive results qualitatively explains Overflow Metabolism.

Quantitative agreement is achieved through the analysis of the heterogeneity of the metabolic status within a cell population. By introducing heterogeneity, the critical growth rate is assumed to follow a Gaussian distribution over the cell population, resulting in accordance with experimental data for E. coli. Overflow metabolism is explained by considering optimal protein allocation and cell heterogeneity.

The obtained model is extensively tested through perturbations: 1) Introduction of overexpression of useless proteins; 2) Studying energy dissipation; 3) Analysis of the impact of translation inhibition with different sub-lethal doses of chloramphenicol on Escherichia coli; 4) Alteration of nutrient categories of carbon sources using pyruvate. All model perturbations results are corroborated by E. coli experimental results.

Strengths:

In this work, the author effectively uses modeling techniques typical of Physics to address complex problems in Biology, demonstrating the potential of interdisciplinary approaches to yield novel insights. The use of Escherichia coli as a model organism ensures that the assumptions and approximations are well-supported in existing literature. The model is convincingly constructed and aligns well with experimental data, lending credibility to the findings. In this version, the extension of results from bacteria to yeast and cancer is substantiated by a literature base, suggesting that these findings may have broad implications for understanding diverse biological systems.

We appreciate the reviewer’s exceptionally positive comments. The manuscript has been significantly improved thanks to the reviewer’s insightful suggestions.

Weaknesses:

The author explores the generalization of their results from bacteria to cancer cells and yeast, adapting the metabolic network and coarse-grained model accordingly. In previous version this generalization was not completely supported by references and data from the literature. This drawback, however, has been treated in this current version, where the authors discuss in much more detail and give references supporting this generalization.

We appreciate the reviewer’s recognition of our revisions and the insightful suggestions provided in the previous round, which have greatly strengthened our manuscript.

Reviewer #2 (Public Review):

In this version of manuscript, the author clarified many details and rewrote some sections. This substantially improved the readability of the paper. I also recognized that the author spent substantial efforts in the Appendix to answer the potential questions.

We thank the reviewer for the positive comments and the suggestions to improve our manuscript.

Unfortunately, I am not currently convinced by the theory proposed in this paper. In the next section, I will first recap the logic of the author and explain why I am not convinced. Although the theory fits many experimental results, other theories on overflow metabolism are also supported by experiments. Hence, I do not think based on experimental data we could rule in or rule out different theories.

We thank the reviewer for both the critical and constructive comments. 

Regarding the comments on the comparison between theoretical and experimental results, we would like to first emphasize that no prior theory has resolved the conflict arising from the proteome efficiencies measured in E. coli and eukaryotic cells. Specifically, prevalent explanations (Basan et al., Nature 528, 99–104 (2015); Chen and Nielsen, PNAS 116, 17592–17597 (2019)) hold that overflow metabolism results from proteome efficiency in fermentation consistently being higher than that in respiration. While it was observed in E. coli that proteome efficiency in fermentation exceeds that in respiration when cells were cultured in lactose at saturated concentrations (Basan et al., Nature 528, 99-104 (2015)), more recent findings (Shen et al., Nature Chemical Biology 20, 1123–1132 (2024)) show that the measured proteome efficiency in respiration is actually higher than in fermentation for many yeast and cancer cells, despite the presence of aerobic glycolytic fermentation flux. To the best of our knowledge, no prior theory has explained these contradictory experimental results. Notably, our theory resolves this conflict and quantitatively explains both sets of experimental observations (Basan et al., Nature 528, 99-104 (2015); Shen et al., Nature Chemical Biology 20, 1123–1132 (2024)) by incorporating cell heterogeneity and optimizing cell growth rate through protein allocation. 

Furthermore, rather than merely fitting the experimental results, as explained in Appendices 6.2, 8.1-8.2 and summarized in Appendix-tables 1-3, nearly all model parameters important for our theoretical predictions for E. coli were derived from in vivo and in vitro biochemical data reported in the experimental literature. For comparisons between model predictions and experimental results for yeast and cancer cells (Shen et al., Nature Chemical Biology 20, 1123–1132 (2024)), we intentionally derived Eq. 6 to ensure an unbiased comparison.

Finally, in response to the reviewer’s suggestion, we have revised the expressions in our manuscript to present the differences between our theory and previous theories in a more modest style. 

Recap: To explain the origin of overflow metabolism, the author uses the following logic:

(1) There is a substantial variability of single-cell growth rate

(2) The flux (J_r^E) and (J_f^E) are coupled with growth rate by Eq. 3

(3) Since growth rate varies from cells to cells, flux (J_r^E) and (J_f^E) also varies (4) The variabilities of above fluxes in above create threshold-analog relation, and hence overflow metabolism.

We thank the reviewer for the clear summary. We apologize for not explaining some points clearly enough in the previous version of our manuscript, which may have led to misunderstandings. We have now revised the relevant content in the manuscript to clarify our reasoning. Specifically, we have applied the following logic in our explanation:

(a) The solution for the optimal growth strategy of a cell under a given nutrient condition is a binary choice between respiration and fermentation, driven by comparing their proteome efficiencies (ε_r and ε_f ).

(b) Under nutrient-poor conditions, the nutrient quality (κ_A) is low, resulting in the proteome efficiency of respiration being higher than that of fermentation (i.e., ε_r > ε_f), so the cell exclusively uses respiration.  

(c) In rich media (with high κ_A), the proteome efficiency of fermentation increases more rapidly and surpasses that of respiration (i.e., ε_f > ε_r ), hence the cell switches to fermentation.  

(d) Heterogeneity is introduced: variability in the κ_cat of catalytic enzymes from cell to cell. This leads to heterogeneity (variability) in ε_r and ε_f within a population of cells under the same nutrient condition.  

(e) The critical value of nutrient quality for the switching point (, where ε_r= ε_f ) changes from a single point to a distribution due to cell heterogeneity. This results in a distribution of the critical growth rate λ_C (defined as ) within the cell population.

(f) The change in culturing conditions (with a highly diverse range of κ_A) and heterogeneity in the critical growth rate λ_C (a distribution of values) result in the threshold-analog relation of overflow metabolism at the cell population level.

Steps (a)-(c) were applied to qualitatively explain the origin of overflow metabolism, while steps (d)-(f) were further used to quantitatively explain the threshold-analog relation observed in the data on overflow metabolism.

Regarding the reviewer’s recap, which seems to have involved some misunderstandings, we first emphasize that the major change in cell growth rate for the threshold-analog relation of overflow metabolism—particularly as it pertains to logic steps (1), (3) and (4)—is driven by the highly varied range of nutrient quality (κ_A) in the culturing conditions, rather than by heterogeneity between cells. For the batch culture data, the nutrient type of the carbon source differs significantly (e.g., Fig.1 in Basan et al., Nature 528, 99-104 (2015), wild-type strains). In contrast, for the chemostat data, the concentration of the carbon source varies greatly due to the highly varied dilution rate (e.g., Table 7 in Holms, FEMS Microbiology Reviews 19, 85-116 (1996)). Both of these factors related to nutrient conditions are the major causes of the changes in cell growth rate in the threshold-analog relation. 

Second, Eq. 3, as mentioned in logic step (2), represents a constraint between the fluxes ( and ) and the growth rate (λ) for a single nutrient condition (with a given value of κ_A ideally) rather than for varied nutrient conditions. For a single cell in each nutrient condition, the optimal growth strategy is binary, between respiration and fermentation. 

Finally, for the threshold-analog relation of overflow metabolism, the switch from respiration to fermentation is caused by the increased nutrient quality in the culturing conditions, rather than by cell heterogeneity as indicated in logic step (4). Upon nutrient upshifts, the proteome efficiency of fermentation surpasses that of respiration, causing the optimal growth strategy for the cell to switch from respiration to fermentation. The role of cell heterogeneity is to transform the growth rate-dependent fermentation flux in overflow metabolism from a digital response to a threshold-analog relation under varying nutrient conditions.

My opinion:

The logic step (2) and (3) have caveats. The variability of growth rate has large components of cellular noise and external noise. Therefore, variability of growth rate is far from 100% correlated with variability of flux (J_r^E) and (J_f^E) at the single-cell level. Single-cell growth rate is a complex, multivariate functional, including (Jr^E) and (J_f^E) but also many other variables. My feeling is the correlation could be too low to support the logic here.

One example: ribosomal concentration is known to be an important factor of growth rate in bulk culture. However, the "growth law" from bulk culture cannot directly translate into the growth law at single-cell level [Ref1,2]. This is likely due to other factors (such as cell aging, other muti-stability of cellular states) are involved.

Therefore, I think using Eq.3 to invert the distribution of growth rate into the distribution of (Jr^E) and (J_f^E) is inapplicable, due to the potentially low correlation at single-cell level. It may show partial correlations, but may not be strong enough to support the claim and create fermentation at macroscopic scale.

Overall, if we track the logic flow, this theory implies overflow metabolism is originated from variability of k_cat of catalytic enzymes from cells to cells. That is, the author proposed that overflow metabolism happens macroscopically as if it is some "aberrant activation of fermentation pathway" at the single-cell level, due to some unknown partially correlation from growth rate variability.

We thank the reviewer for raising these questions and for the insights. We apologize for any lack of clarity in the previous version of our manuscript that may have caused misunderstandings. We have revised the manuscript to address all points, and below are our responses to the questions, some of which seem to involve misunderstandings. 

First, in our theory, the qualitative behavior of overflow metabolism—where cells use respiration under nutrient-poor conditions (low growth rate) and fermentation in rich media (high growth rate)—does not arise from variability between cells, as the reviewer seems to have interpreted. Instead, it originates from growth optimization through optimal protein allocation under significantly different nutrient conditions. Specifically, the proteome efficiency of fermentation is lower than that of respiration (i.e. ε_f < ε_r) under nutrient-poor conditions, making respiration the optimal strategy in this case. However, in rich media, the proteome efficiency of fermentation surpasses that of respiration (i.e. ε_f < ε_r), leading the cell to switch to fermentation for growth optimization. To implement the optimal strategy, as clarified in the revised manuscript and discussed in Appendix 2.4, a cell should sense and compare the proteome efficiencies between respiration and fermentation, choosing the pathway with the higher efficiency, rather than sensing the growth rate, which can fluctuate due to stochasticity. Regarding the role of cell heterogeneity in overflow metabolism, as discussed in our previous response, it is twofold: first, it quantitatively illustrates the threshold-analog response of growth rate-dependent fermentation flux, which would otherwise be a digital response without heterogeneity during growth optimization; second, it enables us to resolve the paradox in proteome efficiencies observed in E. coli and eukaryotic cells, as raised by Shen et al. (Shen et al., Nature Chemical Biology 20, 1123–1132 (2024)). 

Second, regarding logic step (2) in the recap, the reviewer thought we had coupled the growth rate (λ) with the respiration and fermentation fluxes ( and ) through Eq. 3, and used Eq. 3 to invert the distribution of growth rate into the distribution of respiration and fermentation fluxes. We need to clarify that Eq. 3 represents the constraint between the fluxes and the growth rate under a single nutrient condition, rather than describing the relation between growth rate and the fluxes ( and ) under varied nutrient conditions. In a given nutrient condition (with a fixed value of κ_A), without considering optimal protein allocation, the cell growth rate varies with the fluxes according to Eq.3 by adjusting the proteome allocation between respiration and fermentation (ϕ_r and ϕ_f). However, once growth optimization is applied, the optimal protein allocation strategy for a cell is limited to either pure respiration (with ϕ_f =0 and ) or pure fermentation (with ϕ_r =0 and ), depending on the nutrient condition (or the value of κ_A). Furthermore, under varying nutrient conditions (with different values of κ_A), both proteome efficiencies of respiration and fermentation (ε_r and (ε_f) change with nutrient quality κ_A (see Eq. 4). Thus, Eq. 3 does not describe the relation between growth rate (λ) and the fluxes ( and ) under nutrient variations.

Thirdly, regarding reviewer’s concerns on logic step (3) in the recap, as well as the example where ribosome concentration does not correlate well with cell growth rate at the single-cell level, we fully agree with reviewer that, due to factors such as stochasticity and cell cycle status, the growth rate fluctuates constantly for each cell. Consequently, it would not be fully correlated with cell parameters such as ribosome concentration or respiration/fermentation flux. We apologize for our oversight in not discussing suboptimal growth conditions in the previous version of the manuscript. In response, we have added a paragraph to the discussion section and a new Appendix 2.4, titled “Dependence of the model on optimization principles,” to address these issues in detail. Specifically, recent experimental studies (Dai et al., Nature microbiology 2, 16231 (2017); Li et al., Nature microbiology 3, 939–947 (2018)) show that the inactive portion of ribosomes (i.e., ribosomes not bound to mRNAs) can vary under different culturing conditions. The reviewer also pointed out that ribosome concentration does not correlate well with cell growth rate at single-cell level. In this regard, we have cited Pavlou et al. (Pavlou et al., Nature Communications 16, 285 (2025)) instead of the references provided by the reviewer (Ref1 and Ref2), with our rationale outlined in the final section of the author response. These findings (Dai et al, (2017); Li et al., (2018); Pavlou et al., (2025)) suggest that ribosome allocation may be suboptimal under many culturing conditions, likely as cells prepare for potential environmental changes (Li et al., Nature microbiology 3, 939–947 (2018)). However, since our model's predictions regarding the binary choice between respiration and fermentation are based solely on comparing proteome efficiency between these two pathways, the optimal growth principle in our model can be relaxed. Specifically, efficient protein allocation is required only for enzymes rather than ribosomes, allowing our model to remain applicable under suboptimal growth conditions. Furthermore, protein allocation via the ribosome occurs at the single-cell level rather than at the population level. The strong linear correlation between ribosomal concentration and growth rate at the population level under nutrient variations suggests that each cell optimizes its protein allocation individually. Therefore, the principle of growth optimization still applies to individual cells, although factors like stochasticity, nutrient variation preparations, and differences in cell cycle stages may complicate this relationship, resulting in only a rough linear correlation between ribosome concentration and growth rate at the single-cell level (with with R² = 0.64 reported in Pavlou et al., (2025)). 

Lastly, regarding the reviewer concerns about the heterogeneity of fermentation and respiration at macroscopic scale, we first clarify in the second paragraph of this response that the primary driving force for cells to switch from respiration to fermentation in the context of overflow metabolism is the increased nutrient quality under varying culturing conditions, which causes the proteome efficiency of fermentation to surpass that of respiration. Under nutrient-poor conditions, our model predicts that all cells use respiration, and therefore no heterogeneity for the phenotype of respiration and fermentation arises in these conditions. However, in a richer medium, particularly one that does not provide optimal conditions but allows for an intermediate growth rate, our model predicts that some cells opt for fermentation while others continue with respiration due to cell heterogeneity (with ε_f > ε_r for some cells engaging in fermentation and ε_r > ε_f for the other cells engaging in respiration within the same medium). Both of these predictions have been validated in isogenic singlecell experiments with E. coli (Nikolic et al., BMC Microbiology 13, 258 (2013)) and S. cerevisiae (Bagamery et al., Current Biology 30, 4563–4578 (2020)). The single-cell experiments by Nikolic et al. with E. coli in a rich medium of intermediate growth rate clearly show a bimodal distribution in the expression of genes related to overflow metabolism (see Fig. 5 in Nikolic et al., BMC Microbiology 13, 258 (2013)), where one subpopulation suggests purely fermentation, while the other suggests purely respiration. In contrast, in a medium with lower nutrient concentration (and consequently lower nutrient quality), only the respirative population exists (see Fig. 5 in Nikolic et al., BMC Microbiology 13, 258 (2013)). These experimental results from E. coli (Nikolic et al., BMC Microbiology 13, 258 (2013)) are fully consistent with our model predictions. Similarly, the single-cell experiments with S. cerevisiae by Bagamery et al. clearly identified two subpopulations of cells with respect to fermentation and respiration in a rich medium, which also align well with our model predictions regarding heterogeneity in fermentation and respiration within a cell population in the same medium.

Compared with other theories, this theory does not involve any regulatory mechanism and can be regarded as a "neutral theory". I am looking forward to seeing single cell experiments in the future to provide evidences about this theory.

We thank the reviewer for raising these questions and for the valuable insights. Regarding the regulatory mechanism, we have now added a paragraph in the discussion section of our manuscript and Appendix 2.4 to address this point. Specifically, our model predicts that a cell can implement the optimal strategy by directly sensing and comparing the proteome efficiencies of respiration and fermentation, choosing the pathway with the higher efficiency. At the gene regulatory level, a growing body of evidence suggests that the cAMP-CRP system plays an important role in sensing and executing the optimal strategy between respiration and fermentation (Basan et al., Nature 528, 99-104 (2015); Towbin et al., Nature Communications 8, 14123 (2017); Valgepea et al., BMC Systems Biology 4, 166 (2010); Wehrens et al., Cell Reports 42, 113284 (2023)). However, it has also been suggested that the cAMP-CRP system alone is insufficient, and additional regulators may need to be identified to fully elucidate this mechanism (Basan et al., Nature 528, 99-104 (2015); Valgepea et al., BMC Systems Biology 4, 166 (2010)). 

Regarding the single-cell experiments that provide evidence for this theory, we have shown in the previous paragraphs of this response that the heterogeneity between respiration and fermentation, as predicted by our model for isogenic cells within the same culturing condition, has been fully validated by single-cell experiments with E. coli (Fig. 5 from Nikolic et al., BMC Microbiology 13, 258 (2013)) and S. cerevisiae (Fig. 1 and the graphical abstract from Bagamery et al., Current Biology 30, 4563–4578 (2020)). We have now revised the discussion section of our manuscript to make this point clearer.

[Ref1] https://www.biorxiv.org/content/10.1101/2024.04.19.590370v2

[Ref2] https://www.biorxiv.org/content/10.1101/2024.10.08.617237v2

We thank the reviewer for providing insightful references. Regarding the two specific references, Ref1 directly addresses the deviation in the linear relationship between growth rate and ribosome concentration (“growth law”) at the single-cell level. However, since the authors of Ref1 determined the rRNA abundance in each cell by aligning sequencing reads to the genome, this method inevitably introduces a substantial amount of measurement noise. As a result, we chose not to cite or discuss this preprint in our manuscript. Ref2 appears to pertain to a different topic, which we suspect may be a copy/paste error. Based on the reviewer’s description and the references in Ref1, we believe the correct Ref2 should be Pavlou et al., Nature Communications 16, 285 (2025) (with the biorxiv preprint link: https://www.biorxiv.org/content/10.1101/2024.04.26.591328v1). In this reference, it is stated that the relationship between ribosome concentration and growth rate only roughly aligns with the “growth law” at the single-cell level (with R² = 0.64), exhibiting a certain degree of deviation. We have now cited and incorporated the findings of Pavlou et al. (Pavlou et al., Nature Communications 16, 285 (2025)) in both the discussion section of our manuscript and Appendix 2.4. Overall, we agree with Pavlou et al.’s experimental results, which suggest that ribosome concentration does not exhibit a strong linear correlation with cell growth rate at the single-cell level. However, we remain somewhat uncertain about the extent of this deviation, as Pavlou et al.’s experimental setup involved alternating nutrients between acetate and glucose, and the lapse of five generations may not have been long enough for the growth to be considered balanced. Furthermore, as observed in Supplementary Movie 1 of Pavlou et al., some of the experimental cells appeared to experience growth limitations due to squeezing pressure from the pipe wall of the mother machine, which could further increase the deviation from the “growth law” at the single-cell level.  

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I have no specific comments for the authors related to this last version of the paper. I believe the authors have properly improved the previous version of the manuscript.

Response: We thank the reviewer for the highly positive comments and for recognizing the improvements made in the revised version of our manuscript.

Author response:

We thank the reviewers for their thorough review of our manuscript and their constructive feedback. We will address their comments and concerns in a point-by-point response at a later stage but would like to clarify some minor misunderstanding to not confuse any readers in the meantime.

- In regard to population ablation: When investigating the contribution of population size to reconstruction quality, we used 12.5, 25, 50 or 100% of the recorded neuronal population, which corresponds to ~1000/2000/4000/8000 neurons per animal. We did not produce reconstructions from only 1 neuron.

- In regard to the training of the transparency masks: The transparency masks were not produced using the same movies we reconstructed. We apologize for the lack of clarity on this point in the manuscript. We calculated the masks using an original model instance rather than a retrained instances used in the rest of the paper. Specifically, the masks were calculated using the original model instance ‘fold 1’ and data fold 1, which is it’s validation fold. In contrast, the model instances used in the paper for movie reconstruction were retrained while omitting the same validation fold across all instances (fold 0) and all the reconstructed movies in the paper are from data fold 0.

- In regard to reconstruction based on predicted activity: We always reconstructed the videos based on the true neural responses not the predicted neural response, with the exception of the Gaussian noise and drifting grating stimuli in Figure 4 and Supplementary Figure S2 where no recorded neural activity was available).

Author response:

We thank both reviewers for their suggestions on improving our manuscript, which is focused on demonstrating that the C3a-C3aR axis modulates trained immune responses in alveolar macrophages. The Short Report format precludes separating the Results and Discussion sections. However, we will work towards a clearer presentation of findings and providing a more comprehensive interpretation of the data in the Revision, by addressing the points brought up by both Reviewers.

We agree with the suggestions from Reviewer 1 that (1) other cell types such as dendritic cells, neutrophils, and endothelial cells can also be involved in immune training, and (2) macrophages have other activities beyond releasing inflammatory cytokines, and will clarify both these points in the Revision. The mechanism of C3 being cleaved intracellularly and binding to lysosomal C3aR involves cathepsin-dependent cleavage of C3 to C3a and has been experimentally proven (Liszewski et al. Immunity 2013). However, we will clarify this mechanism in the revision. We also acknowledge that the observations need to be validated in human-based models. Currently, we do not have access to an adequate representation of human alveolar macrophages for our ex vivo testing to account for individual-level variation in immune responses. However, we anticipate this work will form the basis of these future studies.

We also appreciate Reviewer 2’s suggestions regarding demonstrating the resolution of acute inflammation after the initial exposure to heat-killed Pseudomonas. We will address this critique by performing additional experiments, which will be included in the Revision. We also agree that the responses of trained C3-deficient cells should be compared to untrained C3-deficient controls after the LPS challenge. We will include this data in the Revision, in addition to the requested data for Figures 3 and 4. We would like to clarify that we do not observe baseline differences between untrained C3-sufficient (wildtype) and C3-deficient alveolar macrophages, even in their glycolytic capacity, and thus, anticipate that our revised data will strengthen the conclusions from the original manuscript.

Author response:

Reviewer #1 (Public review):

Summary:

The authors aimed to characterize neurocomputational signals underlying interpersonal guilt and responsibility. Across two studies, one behavioral and one fMRI, participants made risky economic decisions for themselves or for themselves and a partner; they also experienced a condition in which the partners made decisions for themselves and the participant. The authors also assessed momentary happiness intermittently between choices in the task. Briefly, results demonstrated that participants' self-reported happiness decreased after disadvantageous outcomes for themselves and when both they and their partner were affected; this effect was exacerbated when participants were responsible for their partner's low outcome, rather than the opposite, reflecting experienced guilt. Consistent with previous work, BOLD signals in the insula correlated with experienced guilt, and insula-right IFG connectivity was enhanced when participants made risky choices for themselves and safe choices for themselves and a partner.

Strengths:

This study implements an interesting approach to investigating guilt and responsibility; the paradigm in particular is well-suited to approach this question, offering participants the chance to make risky v. safe choices that affect both themselves and others. I appreciate the assessment of happiness as a metric for assessing guilt across the different task/outcome conditions, as well as the implementation of both computational models and fMRI.

We thank Reviewer 1 for their positive assessment of our manuscript.

Weaknesses:

In spite of the overall strengths of the study, I think there are a few areas in which the paper fell a bit short and could be improved.

We are looking forward to improving our manuscript based on the Reviewers’ comments. According to eLife’s policy, here are our provisional replies as well as plans for changes.

(1) While the framing and goal of this study was to investigate guilt and felt responsibility, the task implemented - a risky choice task with social conditions - has been conducted in similar ways in past research that were not addressed here. The novelty of this study would appear to be the additional happiness assessments, but it would be helpful to consider the changes noted in risk-taking behavior in the context of additional studies that have investigated changes in risky economic choice in social contexts (e.g., Arioli et al., 2023 Cerebral Cortex; Fareri et al., 2022 Scientific Reports).

We certainly agree that several previously published studies have relied on risky choice tasks with social conditions. We will happily refer to the studies mentioned when discussing changes in risk-taking behaviour in our revised manuscript.

(2) The authors note they assessed changes in risk preferences between social and solo conditions in two ways - by calculating a 'risk premium' and then by estimating rho from an expected utility model. I am curious why the authors took both approaches (this did not seem clearly justified, though I apologize if I missed it). Relatedly, in the expected utility approach, the authors report that since 'the number of these types of trials varied across participants', they 'only obtained reliable estimates for [gain and loss] trials in some participants' - in study 1, 22 participants had unreliable estimates and in study 2, 28 participants had unreliable estimates. Because of this, and because the task itself only had 20 gains, 20 losses, and 20 mixed gambles per condition, I wonder if the authors can comment on how interpretable these findings are in the Discussion. Other work investigating loss aversion has implemented larger numbers of trials to mitigate the potential for unreliable estimates (e.g., Sokol-Hessner et al., 2009).

We agree that we have not clearly justified why we have taken two approaches to assess risk preferences. In short, both approaches have advantages and inconveniences when applied to our experiment. We will happily detail our reasons in the revised manuscript. Regarding the second point of this comment: the small number of reliable estimates is one of the reasons that we have used another approach to assess risk preferences. We would certainly have obtained more reliable estimates if we had implemented more trials. We will discuss the interpretability of all the risk preference estimates we used in the revised Discussion.

(3) One thing seemingly not addressed in the Discussion is the fact that the behavioral effect did not replicate significantly in study 2.

We agree that we could have discussed more the fact that there were (slight but significant) differences in risk preferences between the Solo and Social conditions in Study 1 but not in Study 2. While the absence of a significant difference in Study 2 is helpful to compare the neural mechanisms involved in making decisions for oneself vs. for oneself and another person (because any differences could not be explained by differences in risk preferences), we certainly should expand our discussion of the differences in findings between the two studies, which we will do in the revised manuscript.

(4) Regarding the computational models, the authors suggest that the Reponsibility and Responsibility Redux models provided the best fit, but they are claiming this based on separate metrics (e.g., in study 1, the redux model had the lowest AIC, but the responsibility only model had the highest R^2; additionally, the basic model had the lowest BIC). I am wondering if the authors considered conducting a direct model comparison to statistically compare model fits.

We agree that we should run formal, direct model comparison tests using for example chi-square or log-likelihood-ratio tests. We will do so in the revised manuscript.

(5) In the reporting of imaging results, the authors report in a univariate analysis that a small cluster in the left anterior insula showed a stronger response to low outcomes for the partner as a result of participant choice rather than from partner choice. It then seems as though the authors performed small volume correction on this cluster to see whether it survived. If that is accurate, then I would suggest that this result be removed because it is not recommended to perform SVC where the volume is defined based on a result from the same whole-brain analysis (i.e., it should be done a priori).

As indicated in the manuscript, the small insula cluster centered at [-28 24 -4] and shown in Figure 4F survived corrections for multiple tests within the anatomically-defined anterior insula (based on the anatomical maximum probability map described in Faillenot et al., 2017), which is independent of the result of our analysis. We agree that one should not (and we did not) perform multiple corrections based on the results one is correcting – that would indeed be circular and misleading “double-dipping”. The anterior insula is one of the regions most frequently associated with guilt (see the explanations in our Introduction, which refers for example to Bastin et al., 2016; Lamm & Singer, 2010; Piretti et al., 2023). Thus we feel that performing small-volume correction within the anatomically-defined anterior insula is an acceptable approach to correct for multiple tests in this case. We fully acknowledge that, independently of any correction, the effect and the cluster are small. We will clarify these explanations in the revised manuscript.

Reviewer #2 (Public review):

Summary

This manuscript focuses on the role of social responsibility and guilt in social decision-making by integrating neuroimaging and computational modeling methods. Across two studies, participants completed a lottery task in which they made decisions for themselves or for a social partner. By measuring momentary happiness throughout the task, the authors show that being responsible for a partner's bad lottery outcome leads to decreased happiness compared to trials in which the participant was not responsible for their partner's bad outcome. At the neural level, this guilt effect was reflected in increased neural activity in the anterior insula, and altered functional connectivity between the insula and the inferior frontal gyrus. Using computational modeling, the authors show that trial-by-trial fluctuations in happiness were successfully captured by a model including participant and partner rewards and prediction errors (a 'responsibility' model), and model-based neuroimaging analyses suggested that prediction errors for the partner were tracked by the superior temporal sulcus. Taken together, these findings suggest that responsibility and interpersonal guilt influence social decision-making.

Strengths

This manuscript investigates the concept of guilt in social decision-making through both statistical and computational modeling. It integrates behavioral and neural data, providing a more comprehensive understanding of the psychological mechanisms. For the behavioral results, data from two different studies is included, and although minor differences are found between the two studies, the main findings remain consistent. The authors share all their code and materials, leading to transparency and reproducibility of their methods.

The manuscript is well-grounded in prior work. The task design is inspired by a large body of previous work on social decision-making and includes the necessary conditions to support their claims (i.e., Solo, Social, and Partner conditions). The computational models used in this study are inspired by previous work and build on well-established economic theories of decision-making. The research question and hypotheses clearly extend previous findings, and the more traditional univariate results align with prior work.

The authors conducted extensive analyses, as supported by the inclusion of different linear models and computational models described in the supplemental materials. Psychological concepts like risk preferences are defined and tested in different ways, and different types of analyses (e.g., univariate and multivariate neuroimaging analyses) are used to try to answer the research questions. The inclusion and comparison of different computational models provide compelling support for the claim that partner prediction errors indeed influence task behavior, as illustrated by the multiple model comparison metrics and the good model recovery.

We thank Reviewer 2 very much for their comprehensive description of our study and the positive assessment of our study and approach.

Weaknesses

As the authors already note, they did not directly ask participants to report their feelings of guilt. The decrease in happiness reported after a bad choice for a partner might thus be something else than guilt, for example, empathy or feelings of failure (not necessarily related to guilt towards the other person). Although the patterns of neural activity evoked during the task match with previously found patterns of guilt, there is no direct measure of guilt included in the task. This warrants caution in the interpretation of these findings as guilt per se.

We fully agree that not directly asking participants about feelings of guilt is a clear limitation of our study. While we already mention this in our Discussion, we will happily expand our discussion of the consequences on interpretation of our results along the lines described by the reviewer in the revised manuscript. We would like to thank Reviewer 2 for proposing these lines of thought.

As most comparisons contrast the social condition (making the decision for your partner) against either the partner condition (watching your partner make their decision) or the solo condition (making your own decision), an open question remains of how agency influences momentary happiness, independent of potential guilt. Other open questions relate to individual differences in interpersonal guilt, and how those might influence behavior.

We fully agree that the way agency influences happiness has not been much discussed in our manuscript so far, and we would happily do so in the revised manuscript. The same goes for individual differences in interpersonal guilt which we have not investigated due to our relatively small sample sizes but would certainly be worth investigation in subsequent work.

This manuscript is an impressive combination of multiple approaches, but how these different approaches relate to each other and how they can aid in answering slightly different questions is not very clearly described. The authors could improve this by more clearly describing the different methods and their added value in the introduction, and/or by including a paragraph on implications, open questions, and future work in the discussion.

We again thank the reviewer for their praise of our approach and fully agree that we can improve the description of the benefit of combining methods in the Introduction, which we will do in the revised manuscript. We will also include a paragraph on implications, open questions, and future work in the Discussion of the revised manuscript.

However, taken together, this study provides useful insights into the neural and behavioral mechanisms of responsibility and guilt in social decision-making, and how they influence behavior.

We again thank Reviewer 2 for their attentive reading and thoughtful comments and look forward to submitting our revised and improved manuscript.