Reviewer #1 (Public review):

Summary:

Using sequences of short videos to elicit emotional changes in participants, Malamud & Huys demonstrate how a brief, controlled emotion regulation intervention (distancing) can effectively alter subsequent emotion ratings. The authors employ latent state-space models to capture the trajectories of emotion ratings, leveraging tools from control theory to quantify the intervention's impact on emotion dynamics.

Strengths:

The experiment is well-designed and tailored to the computational modeling approach advanced in the paper. It also relies on a selection of stimuli that were previously validated. Within the constraints of a controlled experiment, the intervention successfully implements a relatively common tool of psychotherapeutic treatment, ensuring its clinical relevance.

The computational modeling is grounded in the well-established framework of dynamical systems and control theory. This foundation offers a conceptually clear formalization along with powerful quantification tools that go beyond previous more data-driven approaches.

Overall, the study presents a coherent approach that bridges concepts from clinical psychology and computational theories, providing a timely stepping stone toward advancing quantified, evidence-based psychological interventions targetting emotion control.

Weaknesses:

A primary limitation of this study, acknowledged by the authors, is its reliance on self-reports of participants' emotional states. Although considerable effort was made to minimize expectation effects, further research is needed to confirm that the observed behavioral changes reflect genuine alterations in emotional states. Additionally, the generalizability of the findings to long-term remediation strategies remains an open question.

Second, the statistical analysis, particularly the computational approach, sometimes lacks sufficient detail and refinement. While I will not elaborate on specific points here, one notable issue is the interpretation of the intrinsic matrix (A). The model-free analysis reveals correlations between emotions at a given time or within an emotional state across time points. However, it does not provide evidence to support lagged interactions across states that would justify non-diagonal elements in A. The other result concerning the dynamics matrix only highlights a trend in the dominant eigenvalue, which is difficult to interpret in isolation. The absence of a statistically significant group x intervention interaction furthermore makes this finding a little compelling. This weakens the study's conclusions about the importance of intrinsic dynamics, as claimed in the title.

Finally, to avoid potential misunderstandings of their work, the authors should be more careful about their use of terms pertaining to the control theory and take the time to properly define them. For example, the "controllability" of emotional states can either denote that those states are more changeable (control theory definition), or, conversely, more tightly regulated (common interpretation, as used in the abstract). This is true for numerous terms (stability, sensitivity, Gramian, etc.) for which no clear definition nor references are provided. Readers unfamiliar with the framework of control theory will likely be at a loss without more guidance.

Reviewer #2 (Public review):

Summary:

In this well-conceived and timely study, the authors assess the controllability of emotions in a quantitative way using the framework of control theory. They use a controlled distancing intervention halfway through an emotion rating task where emotion-inducing short videos from a validated database are shown and find that the intervention enables a better controllability of externally induced emotions in the experimental group.

Strengths:

It is a highly original idea to address the external controllability of emotions using the formal framework of control theory. It is also a very propitious approach to take what could be called a 'micro-therapeutic' perspective which looks at the immediate effect of an intervention instead of the 'macro-therapeutic' mid- or long-term effect of a whole course of therapy.

Weaknesses:

Acquiring data online inevitably gives rise to selection and self-selection effects. This needs to be acknowledged clearly. Exacerbating this, participant remuneration seems low at an amount below the minimum or living wage in Western countries (do the authors know where their participants came from?).

Another concern is that the intervention does not simply take place before the second block begins but is ongoing during the whole of the second block in that it is integrated into the phrasing of the task on each trial. It is therefore somewhat misleading to speak of a period 'after the intervention', and it would have been interesting to assess the effect of this by including a third group where the phrasing does not change, but the floating leaves intervention takes place.

As mentioned in the Limitations section, observation noise was assumed and not estimated. While this is understandable in this case, the effect of this assumption could have been assessed by simulation with varying levels of observation (and process) noise.

Relatedly, the reliance on formal model comparison is unfortunate since the outcome of such comparisons is easily influenced by slight changes to assumptions such as noise levels. An alternative approach would have been to develop a favoured model based on its suitability to address the research question and its ability, established by simulation, to distill relevant changes of behaviour into reliable parameter estimates.

The statistical analyses clearly show the limitations of classical statistical testing with highly complex models of the kind the authors (commendably) use. Hunting for statistically significant interactions in a multivariate repeated-measures design relying on inputs from time series-derived point estimates is a difficult proposition. While the authors make the best of the bad situation they create by using null-hypothesis significance testing, a more promising approach would have been to estimate parameters using a sampler like Stan or PyMC and then draw conclusions based on posterior predictive simulations.

Reviewer #3 (Public review):

Summary:

The manuscript takes a dynamical systems perspective on emotion regulation, meaning that rather than a simplistic model conceptualising regulation as applying to a single emotion (e.g. regulation of sadness), emotion regulation could cause a shift in the dynamics of a whole system of emotions (which are linked mathematically to one another). This builds on the idea that there are 'attractor states' of emotions between which people transition, governed by both the system's intrinsic characteristics (e.g. temporal autocorrelation of a particular emotion/person) and external driving forces (having a stressful week). Conceptually this is a very useful advance because it is very unlikely that emotions are elicited (or reduced) singly, without affecting other emotions. This paper is a timely implementation of these ideas in the context of psychotherapeutic intervention, distancing, which participants were trained (randomised) to perform while watching emotion-inducing videos.

The authors' main conclusion is that distancing both stabilises specific emotional patterns and reduces the impact of external video clips. I would consider these results strong and believable, and to have the potential to impact models of emotion regulation as well as the field's broader views on the mechanisms of psychological therapies.

Strengths:

This paper has very many strengths: I would especially note the authors' very-well-matched active control condition and the robustness of their model comparison approach. One feature of the authors' approach is that they explicitly add noise - not what you typically see in an emotion time-series analysis - which allows participants to make errors in their own subjective ratings (a reasonable thing to assume); this noise can then be smoothed during filtering. In their model comparison approach, they explicitly test whether a true dynamical system explains emotion change/emotion regulation effect on emotions - demonstrating that both intrinsic dynamics and external inputs were needed to explain subjective emotion. Powerfully, they also used this approach to test the differential effects of the treatment groups (see below).

The main result seems quite robust statistically. Verifying the effects of the distancing intervention on emotion, the authors found an interaction between time (pre- to post-intervention) and intervention group (distancing vs. relaxation) suggesting that distancing (but not relaxation) reduced ratings of almost all emotions. Participants allocated to the distancing intervention also showed decreased variability of emotion ratings compared to those in the relaxation intervention (though note this interaction was not significant).

Using a model comparison approach, the authors then demonstrated that whilst the control group was best explained by a model that did not change its dynamics of emotions, the active intervention (distancing) group was best explained by a model that captured both changing emotion dynamics and a changing input weights (influence of the videos) - results confirmed in follow-up analyses. This is convincing evidence that emotion regulation strategies may specifically affect the dynamics of emotions - both their relationships to one another and their susceptibility to changes evoked by external influences.

The authors also perform analyses that suggest their result is not attributable to a demand effect (finding that participants were quicker during the control intervention, which one would expect if they had already decided how to respond in advance of the emotion question). I personally also think a demand effect is unlikely given the robustness of their control intervention (which participants would be just as likely to interpret as mental health-enhancing training as distancing), and I am convinced by the notion that demand effects would be unlikely to elicit their more specific effects on the dynamic quality of emotions.

Weaknesses:

An interesting but perhaps at present slightly confusing aspect of their described results relates to the 'controllability' of emotions, which they define as their susceptibility to external inputs. Readers should note this definition is (as I understand it) quite distinct from, and sometimes even orthogonal to, concepts of emotional control in the emotion literature, which refer to intentional control of emotions (by emotion regulation strategies such as distancing). The authors also use this second meaning in the discussion. Because of the centrality of control/controllability (in both meanings) to this paper, at present it is key for readers to bear these dual meanings in mind for juxtaposed results that distancing "reduces controllability" while causing "enhanced emotional control".

As above the authors use an active control - a relaxation intervention - which is extremely closely matched with their active intervention (and a major strength). However, there was an additional difference between the groups (as I currently understand it): "in the group allocated to the distancing intervention, the phrasing of the question about their feelings in the second video block reminded participants about the intervention, stating: "You observed your emotions and let them pass like the leaves floating by on the stream." I do wonder if the effects of distancing also have been partially driven by some degree of reappraisal (considered a separate emotion regulation strategy) since this reminder might have evoked retrospective changes in ratings.

Not necessarily a weakness, but an unanswered question is exactly how distancing is producing these effects. As the authors point out, there is a possibility that eye-movement avoidance of the more emotionally salient aspects of scenes could be changing participants' exposure to the emotions somewhat. Not discussed by the authors, but possibly relevant, is the literature on differences between emotion types on oculomotor avoidance, which could have contributed to differential effects on different emotions.

Author response:

Reviewer 1:

A primary limitation of this study, acknowledged by the authors, is its reliance on self-reports of participants’ emotional states. Although considerable effort was made to minimize expectation effects, further research is needed to confirm that the observed behavioral changes reflect genuine alterations in emotional states.

Thank you very much for raising this point. We fully agree that self-reported emotional states are inherently subjective and that the ramifications of this need to be clarified in the manuscript. However, we would suggest that the focus on self-report may be a strength rather than a limitation. First, the regularities and rules underlying and determining emotional self-report are of primary importance and interest in their own right, and the work presented here does, we believe, shed light on a rich structure present in multivariate timeseries of subjective self-reports and their response to external inputs. Second, there is no clear definition of what a ”genuine emotion state” might be; particularly if there is a discrepancy with self-reported emotions.

Additionally, the generalizability of the findings to long-term remediation strategies remains an open question.

Yes, we agree that what we have described is limited to a short-term intervention and change.

Whether these changes bear on longer-term changes remains to be assessed. Furthermore, the mechanisms or processes that would support such a maintenance are of substantial interest, and will be the focus of future work.

Second, the statistical analysis, particularly the computational approach, sometimes lacks sufficient detail and refinement. While I will not elaborate on specific points here, one notable issue is the interpretation of the intrinsic matrix (A). The model-free analysis reveals correlations between emotions at a given time or within an emotional state across time points. However, it does not provide evidence to support lagged interactions across states that would justify non-diagonal elements in A. The other result concerning the dynamics matrix only highlights a trend in the dominant eigenvalue, which is difficult to interpret in isolation. The absence of a statistically significant group x intervention interaction furthermore makes this finding a little compelling. This weakens the study’s conclusions about the importance of intrinsic dynamics, as claimed in the title.

We appreciate the reviewer’s detailed feedback on the statistical analysis and interpretation of the intrinsic dynamics matrix. It is true that the model-free analysis as presented focuses on within-state correlations and that we have not provided such model-free evidence for lagged interactions across states. We do note that the model comparison suggested that the intervention caused changes in the full A matrix. This would be unlikely if there had not been meaningful cross-emotion lagged effects. Similarly, inference of the A matrix could have revealed a diagonal matrix, and we preferred not to impose such an assumption a priori, as it is very restrictive. Nevertheless, in the absence of a statistically significant group x intervention interaction, the findings regarding the A matrix are less compelling than those related to the control analyses. While this is likely due to a lack of statistical power, these are important points which we will consider in more detail in the revision.

Finally, to avoid potential misunderstandings of their work, the authors should be more careful about their use of terms pertaining to the control theory and take the time to properly define them. For example, the ”controllability” of emotional states can either denote that those states are more changeable (control theory definition), or, conversely, more tightly regulated (common interpretation, as used in the abstract). This is true for numerous terms (stability, sensitivity, Gramian, etc.) for which no clear definition nor references are provided. Readers unfamiliar with the framework of control theory will likely be at a loss without more guidance.

Thank you for this point. We recognize the potential for misunderstanding due to the dual usage of terms such as ”controllability” and will improve the clarity to avoid any misunderstanding.

Reviewer 2:

Acquiring data online inevitably gives rise to selection and self-selection effects. This needs to be acknowledged clearly. Exacerbating this, participant remuneration seems low at an amount below the minimum or living wage in Western countries (do the authors know where their participants came from?).

Thank you for this point. We certainly agree that different experimental settings can induce different biases, and this is no different for online settings. However, online tasks such as the one used here, have become accepted, and there is now a substantial literature showing that in-lab effects are often well-replicated in online settings (Gillan and Rutledge, 2021) . For the current study, it is not clear that an inperson setting may not induce comparably complex biases, e.g. to do with differences between experimenters. All participants were from the UK. Remuneration rates were comparable to other experimental settings, in keeping with other online studies, UK living wage recommendations, and ultimately determined according to institutional ethical guidance.

Another concern is that the intervention does not simply take place before the second block begins but is ongoing during the whole of the second block in that it is integrated into the phrasing of the task on each trial. It is therefore somewhat misleading to speak of a period ’after the intervention’, and it would have been interesting to assess the effect of this by including a third group where the phrasing does not change, but the floating leaves intervention takes place.

Thank you for this point. We acknowledge that the phrasing of the emotion question in the second block may have influenced the observed effects. Including a third group without the reminder would have provided valuable insights and is an important consideration for future studies. We will acknowledge this limitation.

As mentioned in the Limitations section, observation noise was assumed and not estimated. While this is understandable in this case, the effect of this assumption could have been assessed by simulation with varying levels of observation (and process) noise.

Thank you for this comment. We would like to clarify that both observation noise and process noise were estimated in the analyses. We will ensure this is emphasized better in the revised version to avoid future misunderstandings.

Relatedly, the reliance on formal model comparison is unfortunate since the outcome of such comparisons is easily influenced by slight changes to assumptions such as noise levels. An alternative approach would have been to develop a favoured model based on its suitability to address the research question and its ability, established by simulation, to distill relevant changes of behaviour into reliable parameter estimates.

We agree that model comparison alone is insufficient. This is why we have also included extensive simulations, including posterior predictive checks, and have followed established best-practice procedures (Wilson and Collins, 2019). We have focused on a relatively simple model space to avoid overfitting to the dataset, and hence reduce the risk of spurious findings. While we agree that outcomes will be influenced by underlying assumptions, this would persist with the suggested approach of relying on a favoured model. Simulations themselves rely on predefined structures and noise specifications, which inherently shape parameter recovery and inference. Relying only on a favoured model might risk model misspecification, whereby the model may not actually capture the data, and the parameters intended to capture the intervention effect could be confounded. We will clarify the reasoning behind our approach in the revised version.

The statistical analyses clearly show the limitations of classical statistical testing with highly complex models of the kind the authors (commendably) use. Hunting for statistically significant interactions in a multivariate repeated-measures design relying on inputs from time seriesderived point estimates is a difficult proposition. While the authors make the best of the bad situation they create by using null-hypothesis significance testing, a more promising approach would have been to estimate parameters using a sampler like Stan or PyMC and then draw conclusions based on posterior predictive simulations.

This comment raises several interesting points. First, we agree that the value of classical test on individual parameters within such complex situations is limited. This is why our main focus is on global measures like model comparison. Our use of the classical tests is more to support the understanding of the nature of the data, i.e. they have a more descriptive aim. We will hope to clarify this further in the revision. Second, in terms of sampling, we would like to emphasize that the Kalman filter is both efficient and analytical tractable, making it well-suited to our data and research question. It may have been possible to use sampling to obtain posterior distributions rather than point estimates. However, we did not judge this to be worth the (substantial) additional computational cost.

Reviewer 3:

An interesting but perhaps at present slightly confusing aspect of their described results relates to the ’controllability’ of emotions, which they define as their susceptibility to external inputs. Readers should note this definition is (as I understand it) quite distinct from, and sometimes even orthogonal to, concepts of emotional control in the emotion literature, which refer to intentional control of emotions (by emotion regulation strategies such as distancing). The authors also use this second meaning in the discussion. Because of the centrality of control/controllability (in both meanings) to this paper, at present it is key for readers to bear these dual meanings in mind for juxtaposed results that distancing ”reduces controllability” while causing ”enhanced emotional control”.

We fully agree with the reviewer’s observation that ”controllability” can be interpreted in different ways. we will revise the text to ensure consistent usage and explicitly state the distinction between the control theory definition of controllability and its interpretation in the emotion regulation literature.

As above the authors use an active control - a relaxation intervention - which is extremely closely matched with their active intervention (and a major strength). However, there was an additional difference between the groups (as I currently understand it): ”in the group allocated to the distancing intervention, the phrasing of the question about their feelings in the second video block reminded participants about the intervention, stating: ”You observed your emotions and let them pass like the leaves floating by on the stream.” I do wonder if the effects of distancing also have been partially driven by some degree of reappraisal (considered a separate emotion regulation strategy) since this reminder might have evoked retrospective changes in ratings.

We appreciate this substantial point. While our study was designed to isolate the effects of distancing, we acknowledge that elements of reappraisal may also have influenced the results. We will discuss this in the revised version. Additionally, as noted in our response to Reviewer 2, including a third group without the reminder could have provided valuable information, and we consider this to be an important direction for future research.

Not necessarily a weakness, but an unanswered question is exactly how distancing is producing these effects. As the authors point out, there is a possibility that eye-movement avoidance of the more emotionally salient aspects of scenes could be changing participants’ exposure to the emotions somewhat. Not discussed by the authors, but possibly relevant, is the literature on differences between emotion types on oculomotor avoidance, which could have contributed to differential effects on different emotions.

Thank you very much for these suggestions. It is very true that different emotions can elicit different patterns of oculomotor avoidance, which could have contributed to our observed effects. Research suggests that emotions such as disgust are associated with visual avoidance (Armstrong et al., 2014; Dalmaijer et al., 2021), whereas anxiety and other negative emotions exhibited increased attentional bias after fear conditioning (Kelly and Forsyth, 2009; Pischek-Simpson et al., 2009). It would be very interesting to repeat the experiment with eye-tracking to examine these possibilities. What would be particularly interesting to examine is whether a distancing intervention induces multiple, emotionally-specific behaviours, or not.

References

Armstrong, T., McClenahan, L., Kittle, J., and Olatunji, B. O. (2014). Don’t look now! Oculomotor avoidance as a conditioned disgust response. Emotion (Washington, D.C.), 14(1):95–104.

Dalmaijer, E. S., Lee, A., Leiter, R., Brown, Z., and Armstrong, T. (2021). Forever yuck: Oculomotor avoidance of disgusting stimuli resists habituation. Journal of Experimental Psychology. General, 150(8):1598– 1611.

Gillan, C. M. and Rutledge, R. B. (2021). Smartphones and the Neuroscience of Mental Health. Annual Review of Neuroscience, 44(Volume 44, 2021):129–151. Publisher: Annual Reviews.

Kelly, M. M. and Forsyth, J. P. (2009). Associations between emotional avoidance, anxiety sensitivity, and reactions to an observational fear challenge procedure. Behaviour Research and Therapy, 47(4):331–338. Place: Netherlands Publisher: Elsevier Science.

Pischek-Simpson, L. K., Boschen, M. J., Neumann, D. L., and Waters, A. M. (2009). The development of an attentional bias for angry faces following Pavlovian fear conditioning. Behaviour Research and Therapy, 47(4):322–330.

Wilson, R. C. and Collins, A. G. (2019). Ten simple rules for the computational modeling of behavioral data. eLife, 8:e49547. Publisher: eLife Sciences Publications, Ltd.

eLife Assessment

This important study has modified ChIP-seq and 4C-seq procedures with a urea step and shows that this drastically changes the pattern of chromatin interactions observed for SATB1 but not other proteins (CTCF, Jarid2, Suz12, Ezh2). Multiple controls make the data convincing. The findings shed new light on the role of SATB1 in genome organization and will be of interest to those who study chromosome structure and nuclear organization.

Reviewer #1 (Public review):

Summary:

The nuclear protein SATB-1 was originally identified as a protein of the 'nuclear matrix', an aggregate of nuclear components that arose upon extracting nuclei with high salt. While the protein was assumed to have a global function in chromatin organization, it has subsequently been linked to a variety of pathological conditions, notably cancer. The mapping of the factor by conventional ChIP procedures showed strong enrichment in active, accessible chromatin, suggesting a direct role in gene regulation, perhaps in enhancer-promoter communication. These findings did not explain why SATB-1-chromatin interaction resisted the 2 M salt extraction during early biochemical fractionation of nuclei.

The authors, who have studied SATB-1 for many years, now developed an unusual variation of the ChIP procedure, in which they purify crosslinked chromatin by centrifugation through 8 M urea. Remarkably, while they lose all previously mapped signals for SATB-1 in active chromatin, they now gain many binding events in silent regions of the genome, represented by lamin-associated domains (LADs).

SATB-1 had previously been shown by the authors and others to bind to DNA with special properties, termed BUR (for 'base-unpairing regions'). BURs are AT-rich and apparently enriched in equally AT-rich LADs. The 'urea-ChIP' pattern is essentially complementary to the classical ChIP pattern. The authors now speculate that the previously known SATB-1 binding pattern, which does not overlap BURs particularly well, is due to indirect chromatin binding, whereas they consider the urea-ChIP profile that fits better to the BUR distribution on the chromosome to be due to direct binding.

Building on the success with urea-ChIP the authors adapted the 4C-procedure of chromosome conformation mapping to work with urea-purified chromatin. The data suggest that BUR-bound SATB-1 in heterochromatin mediates long-distance interaction with loci in active chromatin. They close with a model, whereby SATB-1 tethers active chromatin to the nuclear lamina. Because cell type-specific differences are observed, they suggest that the SATB-1 interactions are functionally relevant.

Strengths:

Given the unusual finding of essentially mutually exclusive 'standard ChIP' and 'urea-ChIP' profiles for SATB-1, the authors conducted many appropriate controls. They showed that all SATB-1 peaks in urea-ChIP and 96% of peaks in standard-ChIP represent true signals, as they are not observed in a SATB-1 knockout cell line. They also show that urea-ChIP and standard ChIP yield similar profiles for CTCF. The data appear reproducible, judged by at least two replicates and triangulation. The SATB-1 KO cells provide a nice control for the specificity of signals, including those that arise from their elaborately modified 4C protocol.

Weaknesses:

The weaknesses mainly relate to missing qualifier statements and overinterpretations. I also found some aspects of the model not yet well supported by the data.

(1) Under high urea conditions the BUR elements should be rendered single-stranded, and one wonders whether this has any effect on the procedure. The authors should alert the reader of these circumstances.

(2) An important conclusion is that urea-ChIP reveals direct DNA binding events, whereas standard ChIP shows indirect binding (which is stripped off by urea). I do not yet see any evidence for direct binding. It cannot be excluded, for example, that the binding is RNA-mediated. The authors mention in passing that urea-ChIP material still contains (specific!) RNA. Given that this is a new procedure, the authors should document the RNA content of urea-ChIP and RNase-treat their samples prior to ChIP to monitor an RNA contribution.

(3) An important aspect of the model is that SATB-1 tethers active genes to inactive LADs. However, in the 4C experiment the BUR elements used to anchor the looping are both in the accessible, active chromatin domain.

Reviewer #2 (Public review):

Summary:

The report by Kohwi-Shigematsu et al. describes the key observation that SATB1 binds directly to so-called BUR elements. This is in contrast to several other reports describing SATB1 binding to promoters and enhancers. This discrepancy is explained by the authors to depend on the features of the ChIP technique being used. Urea-ChIP, innovated by the authors, strips off protein-protein interactions that are maintained in conventional ChIP. The authors convincingly make the case that SATB1 and the key genome organiser CTCF co-localize by conventional ChIP but not urea ChIP, as particularly evident in Figure 2A. SATB1 controls long-range interactions in thymocytes and the expression of gene clusters. This feature is independent of TADs, as the knockdown of SATB1 expression does not affect the TAD patterns.

Strengths:

A new and innovative adaptation of the urea ChIP-seq technique has enabled the authors to reveal a new aspect of SATB1 binding to the genome. The authors provide a wealth of data to reinforce their claims. This report thus sheds new light on SATB1 function, which is particularly important given its role in metastasising cancer cells.

Weaknesses:

No weaknesses were identified by this reviewer.

eLife Assessment

This important study investigates the different mechanisms that provide instructions for a missing body part to regenerate its appropriate identity. The authors use two species of planarians to identify a key role for bodywide canonical Wnt gradients in controlling the outcome of regeneration. The study provides convincing evidence for variable regeneration efficiency among planarian species that will be of interest to developmental biologists interested in regeneration. However, some of the results are over-interpreted and the additional experiments could provide better support for the authors' claims.

Reviewer #1 (Public review):

Summary:

In the manuscript entitled 'A comparative analysis of planarian regeneration specificity reveals tissue polarity contributions of the axial cWnt signalling gradient.' Cleland et al. study the robustness of regenerating a head or a tail in the proper position in two different planarian species (S. mediterranea and G. sinensis). The authors find that the expression of notum, a Wnt inhibitor that is triggered after any cut, shows different dynamics of expression in both planarian species, being more symmetrical in the species that display a higher number of double-headed or Janus heads (G. sinenesis), which they refer to a less robust regeneration. The authors claim that the reduced robustness of G. sinensis regeneration is partially explained by this anterior-posterior symmetric expression of notum, since in S. mediterranea, which shows a 'robust regeneration' it appears asymmetric. So, the first claim of the manuscript is that the symmetry in notum expression could underlie the poor robustness of regenerating a head/tail in small bipolar regenerating planarian fragments.

Then, they analyse the role of a proposed tail-to-head cWnt signalling gradient during the regeneration of heads and tails in the same planarian species. To do so they develop an antibody that allows the quantification of b-catenin activity along the AP axis, together with a pharmacological approach that reduces the pre-existent cWnt gradient without affecting the wound-induced. Through this strategy the authors can demonstrate the slope of the b-catenin activity, which is a very nice result, and that it changes according to the size of the animal. Furthermore, they are able to demonstrate that by reducing the cWnt signalling in the pre-existent tissue, there is an increase in the number of double-headed regenerates (Janus heads) and that it depends on the body size and on the decreasing steepness of the cWnt gradient. This result relies on G. sinensis species since the drug is not so effective in S. mediterranea. Thus, the authors' second claim is that the slope of the cWnt gradient may contribute to head-tail regeneration specificity in planarians.

To conclude, it is proposed that regeneration of the correct identity in each wound depends on multiple cues acting in parallel and that their species-specificity provides variations in the regenerative capability of the different planarian species.

The study has great potential to have a high impact on the regeneration community, since the opportunity to compare mechanisms between close species provides the framework for understanding the essential mechanism of regeneration.

Strengths:

The project has several strengths. The authors are able to reproduce the Janus heads phenotypes described by Morgan TH by analysing different planarian species. This is of great importance in the planarian field, because with the current model species, S. mediterranea, this could not be reproduced. So, these results demonstrate that small planarian fragments do make errors during regeneration, giving rise to double-headed animals, which supports the well-known hypothesis that it exists an anteroposterior gradient underlying anteroposterior identity during regeneration. However, and importantly, it does not occur in all planarian species. So, there are differences between planarian species in the robustness of regeneration and may be in the mechanisms that drive this regeneration. The finding of different behaviours and gene expressions in different planarian species is very interesting and promising in the field of regeneration.

A second strength of the study is the demonstration of the b-catenin1 slope in planarians and how it changes with the animal size, and also the establishment of a method to decrease it in the pre-existent tissue but not in the wound. This strategy allows us to examine specifically the role of the pre-existent cWnt signal, demonstrating that it does have a role in the decision of making head or tail during regeneration, which was an essential question in the field of planarians and animal regeneration.

Weaknesses:

(1) The finding that notum, which is the main head determinant identified in planarians, has a different dynamic in both planarian species is very suggestive. However, the different dynamics of notum expression during regeneration, which is the basis of the subsequent rationale, is not properly demonstrated, nor is its correlation with the robustness in regenerating a proper head/tail identity. Main concerns regarding this point:

a) The authors observe that 'In regenerating S. mediterranea 2 mm trunk pieces cut from 6 mm animals, notum expression was induced predominantly at anterior-facing wounds as early as 6 h post-amputation (Figure 2A), as previously reported (Petersen and Reddien 2011)'. However, in the graphics in Figures 2B and C, the expression of notum at 6h is shown as symmetric. It definitely does not agree with the in situ, with the text, or with the published data. How was it measured? It should be corrected and explained since it is the basis of the subsequent rationale.

b) Then, when measuring notum in G. sinensis the authors conclude: 'Strikingly and in sharp contrast to S. mediterranea, the number of notum expressing cells was nearly identical between anterior and posterior wounds without any discernible A/P asymmetry at any of the examined time points (Figures 2E-F)'. However, in the in situ results of 12 h regenerating G. sinensis, there is a clear difference in notum expression between anterior and posterior wounds. Is it not representative of the image? Again, how exactly the measurements were performed? Are dots or pixels quantified? It is not explained in the text. This is a crucial result that has to be consistent.

c) A more general weakness of this part of the manuscript is that even if the authors demonstrate that in G. sinensis the expression of notum is symmetrical in contrast to S. mediterranea, this is just an observation of 1 species that has symmetrical notum and regenerates less robustly than 1 species that has asymmetrical expression and regenerates more robustly. If they for instance look at the expression of wnt1, maybe they also see differences between both species that could be linked to their different regeneration properties (related to this, see below the comment on wnt1 expression). That is to say, comparing 1 to 1 species cannot give any cause-effect evidence.<br /> Furthermore, the authors rely on the fact that notum inhibition rescues the wild-type phenotype to conclude that is the symmetric expression of notum that underlies the appearance of Janus heads. This is what can be read in the results: 'Significantly, the rescue of wild-type regenerates by notum(RNAi) suggests that the symmetric G. sinensis notum expression contributes to the formation of double-heads and thus to reduced regeneration specificity'; and in the Summary: We found that the reduced regeneration robustness of G. sinensis was partially explained by wound site-symmetric expression of the head determinant notum, which is highly anterior-specific in S. mediterranea.' However, notum RNAi decreases notum in both wounds, so it does not produce an asymmetric expression (at least this is not shown). So, it does not link the symmetry or asymmetry of notum with the appearance of Janus heads.

d) If the authors want to maintain the claim that the symmetry of notum is one of the reasons that explain the increase in Janus head phenotype in G. sinensis, there are several possibilities to test it. For instance:

i) Analyse notum expression in different planarian species and relate its symmetry or asymmetry with the appearance of Janus heads. If the claim is true, the species that are more robust should show more asymmetric expression of notum. This would sustain strongly the first claim, and would really be a breakthrough in the field of regeneration.

ii) Another possibility is a more in-depth analysis of notum expression in the species of the study. If the authors show that larger fragments show fewer Janus heads, and also that it depends on the anteroposterior level of the fragments, they could try to relate the rate of Janus heads with the degree of asymmetry in notum expression in both wounds. For instance, they could analyze notum expression in bipolar regenerating fragments along the anteroposterior axis in both species; it should be more symmetric in G sinenesis, in all fragments, according to Figure 2 L. Or they could analyze notum expression in bipolar regenerating fragments of different sizes, mainly in 1 or 2 mm fragments of big planarians, since they are the fragments analyzed that form or not the Janus heads. In G sinensis the expression of notum should be more symmetrical than in S. mediterranea in these fragments.

iii) The authors could design an experiment to demonstrate that the symmetry in the expression of notum affects the rate of Janus heads. The experiment that the authors show is the rescue of the Janus heads in G. sinensis after notum RNAi. However, notum RNAi suppresses notum in both wounds, thus not making them asymmetric. Furthermore, the rescue could be explained by the posteriorizing effect that notum RNAi has in planarians, as reported by several authors. A possibility could be to inhibit APC, which increases notum expression in S. mediterranea (Petersen and Reddien 2011). If APC RNAi in G. sinenesis produces an increase in notum in both wounds and the rate of Janus heads is not rescued, then it would support the hypothesis that notum symmetry is the cause of the Janus heads. However, if it produces an increase of notum in an asymmetric manner, then the Janus phenotype should be rescued.

(2) The second weakness of the study is related to the methodology used to support the second claim, that the slope of bcatenin1 activity has a role in the decision of regeneration - a head and a tail in the correct tip. The main concerns relate to the specificity of the anti-bcatenin1 antibody and to the broad effect of C59 in the secretion of all Wnts.

a) Raising an antibody against beta-catenin1 that allows the quantification by western blot is a strength of the study, since beta-catenin1 is the key element of the cWnt pathway, and their levels are directly associated with the activation of the pathway. Since this is one of the tools that support the second claim of the study, a characterization of the antibody and additional tests to prove its specificity are required. The authors show a Western blot in which the band intensity decreases after beta-catenin1 inhibition in both species. Further analysis should be shown:<br /> i) Demonstration that the intensity of the band increases after APC or Axin inhibition.<br /> ii) Does the antibody work in immunohistochemistry? It would provide further evidence of the specificity of a nuclear signal could be demonstrated.<br /> iii) Explanation and discussion of the protocol used to analyse the levels of b-catenin1 activity along the anteroposterior axis is required. It has been reported that beta-catenin1 is highly expressed and required in the brain in planarians, and also in the pharynx, and in the sexual organs (Hill and Petersen 2015, Sureda-Gomez et al 2016). How is it then explained the anterior-to-posterior gradient of expression of beta-catenin1 seen in this study in both species? Has the pharynx been removed before the protein extraction? What about the beta-catenin1 activity demonstrated in the brain? Why is it not reflected in the western blot analysis using the antibody? This point should be clarified.

b) The second tool used in the second part of the manuscript is the drug C59, which inhibits Porcupine, a protein required for palmitoylation and secretion of Wnts. Because Porcupine could be required for the secretion of all Wnts, the phenotype obtained with the drug could be the sum of the inhibition of cWNT signal (wnt1 for instances) and non-canonical WNT (as wnt5). This is in fact the phenotype resulting after the inhibition of Wntless in planarians (Adell et al. 2009), which is also required for the secretion of Wnts. Thus, in the phenotypes resulting from C59 treatment the analysis of the nervous system and posterior/anterior markers is required. Looking at the in vivo phenotype it appears that in fact the drug is affecting both canonical and no canonical pathways since the animal with protrusions in the lateral part (Figure 4B-double head, or Supplementary Figure 3A) is very similar to the one reported after Wntless inhibition. In case the phenotypes observed also show non-canonical Wnt inhibition, this should be clearly shown and discussed.

The above-mentioned weaknesses are the most important concerns about the present manuscript. However, there are other concerns related to a further analysis of the phenotypes and the analysis of additional Wnt elements as wnt1, which are essential to complete the study and are directly discussed with the authors.

Reviewer #2 (Public review):

Summary:

This study identifies a key role for bodywide canonical Wnt gradients in controlling the outcome of regeneration within planarians, likely acting in parallel to injury-induced cues that also use tissue asymmetry to control this process. In S. Mediterranea a central part of this decision process is the asymmetric expression of the Wnt inhibitor notum specifically at injury sites facing in the anterior direction to promote head formation and inhibit tail formation through regulation of canonical Wnt signaling pathways. Leveraging classic studies by T.H. Morgan over a century ago, which found that amputated thin transverse fragments occasionally incorrectly regenerate 2 heads rather than a head and a tail in a species of Girardia planarians, this study identifies a closely related species G. Sinensis which undergoes errors to regeneration specificity under similar challenges. Morgan had proposed that his results might arise from the use of a "gradient of materials" providing axis information across the body axis such that small tissue fragments are too narrow to interpret gradient differences, leading to head/tail polarity defects in regeneration. The authors show very convincingly that this species of planaria undergoes notum expression after injury, but unlike in S. Mediterranea, this occurs symmetrically at the onset of regeneration. Using RNAi, they show notum participates in the regeneration of mispolarized heads (though interestingly apparently not in normal head regeneration unlike in Smeds, at least under these conditions). G. Sinensis planarians, like many organisms, have abundant expression of Wnt genes posteriorly. To test whether this gradient of Wnts may participate in the regeneration distinct from any Wnt signals activated after injury, the authors use chemical inhibition to reduce Wnt signaling prior to injury and then alleviate inhibition following injury by removal of the drug and confirming successful washout of the drug using mass spec. They also raise a new antibody that can detect beta-catenin-1 in this species in order to monitor the body-wide cWnt gradient after these treatments, and correlate this with outcomes on the head/tail regeneration decision. Using this approach, they find that homeostatic inhibition of porcupine (required for Wnt secretion) could dampen the cWnt/beta-catenin gradient and increase the incidence of inappropriate head regeneration at posterior-facing wounds. In addition, they find that the cWnt gradient is less steep in larger animals that also concurrently have a higher incidence of mistakes in regeneration specificity. Together, the paper presents compelling experiments and analysis to support the conclusion that cWnt gradients are an important determinant of head/tail identity determination decisions in G. Sinensis, and thereby proposes a plausible model that the notum asymmetry present in S. Mediterranea could act in parallel to support the higher regeneration robustness observed in that species.

Strengths:

This is a great paper, an instant classic. It addresses an enduring problem that Morgan and others initiated more than a century ago and brings a new synthesis of ideas to clarify an important mechanism. I also like the term "regeneration specificity" which can provide a nice unification and generalization of ideas that other authors have variously described as regeneration patterning or regeneration polarity. The work is a tour de force that creatively builds new tools and observations to leverage a new model of planarian species for unraveling general mechanisms of regeneration decision-making. The experiments are rigorously conducted and I find the overall data to be quite compelling. I have some comments for the authors to consider below for drawing out the interpretation and also clarifying the underlying mechanism.

Comments:

(1) The G. Sinesis species showed accurate head/tail specificity in 2mm thick fragments but was strongly impaired at 1 mm thick. I am assuming that outcomes of pieces greater than 2mm would make similarly robust head/tail choices, implying a rather sharp transition occurring between 1 and 2 mm. In that case, in the gradient model, are there theoretical reasons to predict that polarity outcomes would decline sharply rather than gradually as size thickness decreases? I think the muscle fibers themselves are thought to have lengths on the order of 200 microns, so I wonder what could account for the characteristic length of less than 1mm here? From the lab's prior analysis of beta-cat gradient, is this perhaps the minimal length where a difference in bcat protein levels can be detected? This is not essential to resolve in this draft (in my view), just a very interesting question arising from the present study. Relatedly, it seems that the slope of cWnt at the wound site itself might not be enough information for polarity because at a highly granular level, this should be identical at posterior-facing wounds from trunk fragments versus thin transverse fragments obtained at the same AP position, yet trunk fragments succeed at regeneration specificity whereas thin transverse fragments fail.

(2) The paper nicely shows strong evidence that notum expression is definitely symmetric at the first occurrence of its expression by 6 hours in D. Sinensis, and this is a really important result of the paper. At 12 hours, it does look to me in the FISH experiments that there is more persistence of expression at the anterior-facing wound versus the posterior-facing wounds (Fig 2D), although the methods for quantification in Fig2E/F do not show a difference in expression at the two wound sites at this time point. Could this difference arise from differences in the perdurance or timing of early wound-induced signaling at the two wound sites that was perhaps too subtle to detect in the quantification methods used? Or perhaps these images do not represent the population? On a related note, the quantification method seems to fail to show that in 6h Smeds, notum expression is indeed asymmetric. Probably the issue here is not the data in the FISH images themselves which strongly support the author's interpretations, but rather a deficiency or limitation of the quantification method used, which should be resolved so that the conclusions from the single FISH images can be interpreted robustly. For example, some authors have used a method of counting notum+ cells and I wonder if this could provide better quantitative information here.

(3) Given that the double-headed phenotype is observed from thin transverse fragments, ideally, the symmetry of notum could be established to occur in those types of fragments as well. This experiment would clarify that notum is expressed at posterior-facing wounds in the very same types of fragments that undergo the highest levels of mistakes in regeneration specificity.

(4) Is wnt1 expressed symmetrically at wound sites in this species? It seems there are cases like acoels where wound-induced Wnt activation can occur asymmetrically but through preferential expression of Wnts at posterior-facing wounds, rather than notum. It would be interesting to know although I also think the work the authors already have done in this study itself already constitutes a very comprehensive advance and could be the subject of future work.

(5) I agree that notum is relatively much more strongly expressed at the far posterior region in D. Senesis than in Smeds, but it does seem from the RNAseq data it also has some locally enriched expression at the anterior pole. Because the RNAseq analysis involves scaling expression across the regions for each gene, it is difficult to know if the anterior expression is relatively lower or perhaps even about the same level of expression as the anterior pole expression of this gene in Smeds. Though not essential to make the desired arguments, in situs on notum in the intact animals would be helpful to clarify this. Relatedly it would be fascinating to know whether D. Senesis notum undergoes anterior-pole expression around the 72 hour or similar timepoint as in Smeds.

(6) The assessment of beta-catenin gradients was done through protein extractions from whole tissue fragments. However, it has been shown in other planarian species that beta-catenin can have strong tissue-specific expression in, for example, the pharynx, brain, and reproductive systems. Some supporting evidence or argument should be presented to clarify the interpretation that the graded expression observed by western blotting cannot be fully explained by this kind of tissue-specific expression of beta-catenin rather than representing a true signaling gradient as interpreted by the authors. For example, if this antibody could be used in immunostaining, this could support the beta-catenin signaling gradient. Alternatively, information about the location of the pharynx or any other posterior reproductive tissues in D. Sinensis could be calibrated with respect to the fragment bins used for the gradient--perhaps a portion of the C59-dependent body-wide gradient measured here occurs fully within tail tissue that lacks other regionalized tissue that could be a potential additional source of beta-catenin. Further discussion and interpretation, or additional experiments, should be included to rule out alternative confounding sources of beta-catenin in order to clarify the interpretation of the western blot as representing a beta-catenin signaling gradient.

(7) I find the analysis in Figure 5 to be quite compelling for showing the importance of cWnt/Bcat gradients in contributing to head/tail determination, and I also think that the author's discussion of the limitations of the approach are well articulated and considered. Based on prior literature, it also seems very likely that there is a third redundantly acting component to regeneration specificity, which is the amplification of small differences in cWnt in a directional-dependent manner early in the regeneration process (24-72 hours in Smeds). This would explain why post-amputation with porcupine inhibitor in D. Sinensis caused 100% penetrant defects in regeneration specificity while the pre-treatment paradigm caused a weaker effect (25-40% for larger animals). In Smeds, it is known already that delivery of dsRNAs against beta-catenin-1, wnt1, and notum only after injury caused polarity defects, and thus all three genes certainly have a function relevant for head/tail after injury (Petersen and Reddien 2008, 2009, 2011- please note these experiments were reported in the text of these studies and not in individual figures). This evidence, combined with extensive FISH and complementary RNAi studies in the field, strongly suggests that some combination of the 6-18h injury-induced phase but also very likely the subsequent "pole-specific phase" of wnt1 expression is likely to be important for driving or enacting the tail fate program and is therefore a component of the regeneration specificity mechanism described here.

(8) Prior work has also demonstrated roles for Wnt genes expressed in gradients to participate in regeneration specificity. In particular, inhibition of the wntP-2/wnt11-5 gene, which is expressed in an animal-wide gradient, strongly enhanced the effects of inhibition of wnt1, which is the earliest wound-activated Wnt gene, to cause 100% penetrant posterior head regeneration phenotypes in S. mediterranea (Petersen and Reddien 2009). These observations are complementary to the present study by implicating Wnts expressed in bodywide gradients in the process of regeneration decision-making. Given that this study also showed that wnt1 is necessary for new wntP-2 expression during the wound-induced early phase and that wnt1 activation does not require beta-catenin for its expression, collectively suggest a more complex process involved in gradient detection and the involvement of wound signals likely beyond only autoregulation of the cWnt gradient or notum asymmetry mechanisms. Although this paper is cited already, framing the present study more fully in context with this and other relevant prior work would be helpful to contextualize the advance for the field.

Reviewer #3 (Public review):

Summary:

In this study, the authors revisit the hypothesis of gradient-based polarity specification during planarian regeneration proposed over a century ago, but here they apply molecular techniques and a valuable comparative approach. By using a comparative analysis with classic and modern planarian model organisms, the authors have identified variable molecular mechanisms that different planarian species utilize to ensure that the proper tissues are regenerated following wounding.

Strengths:

The comparative approach of using 2 different planarian species allowed the study to elucidate different molecular mechanisms that planarians utilize in re-establishing anterior-posterior axis polarity during regeneration. Without this comparative approach, the mystery of T.H. Morgan's data classic studies that demonstrate mistakes in this axis re-polarization would remain unanswered. Furthermore, the use of both a modern molecular model species and another more classical planarian species, which the authors have fully developed with molecular tools and techniques, sheds light on the diversity of genetic processes that closely related species seem to utilize in regeneration. To dissect the role of a long-hypothesized canonical cWnt signaling gradient, the authors developed a novel strategy using chemical genetics to titer this gradient, which led to phenotypes with enhanced aberrant axis polarity re-establishment. Together these experimental approaches establish a well-supported initial model for explaining the molecular mechanisms that different planarian species utilize to allow for proper regeneration of lost tissues.

Weaknesses:

While pharmacological perturbation of signaling pathways could produce off-target effects, the authors provide well-documented evidence that canonical Wnt signaling is altered with drug treatment. The correlation between altered cWnt signaling gradients and the incidence of double-headed regeneration is strong, but it is not clear that the axial cWnt signaling gradient is the ultimate cause of the modified regeneration polarity. However, the model established here and supported by considerable data provides a useful alternative to the mechanism of notum upregulation that has been well-documented in the Schmidtea mediterranea, the workhouse model in planarian research. Throughout the manuscript, the authors suggest that Girardia sinensis lost the ability to upregulate notum at anterior-facing wounds, but until additional planarian species are evaluated, it remains plausible (and equally parsimonious) that S. mediterranea could have innovated a novel strategy to re-establish axis-polarity through asymmetric notum expression.

The study is very well-designed with considerable confirmation of results, especially in the novel use of the pharmacological inhibitor C59. This study is invaluable in its comparative approach, finding that well-established molecular processes may not explain similar developmental outcomes for different species; this corroborates the need to study additional model organisms and how an evolutionary approach to the study of development is imperative.

eLife Assessment

This valuable study reports a potential connection between the seminal microbiome and sperm quality/male fertility. The data are generally convincing. This study will be of interest to clinicians and biomedical researchers who work on microbiome and male fertility.

Reviewer #1 (Public review):

Summary:

The authors analyzed the bacterial colonization of human sperm using 16S rRNA profiling. Patterns of microbiota colonization were subsequently correlated with clinical data, such as spermiogram analysis, presence of reactive oxygen species (ROS), and DNA fragmentation. The authors identified three main clusters dominated by Streptococcus, Prevotella, and Lactobacillus & Gardnerella, respectively, which aligns with previous observations. Specific associations were observed for certain bacterial genera, such as Flavobacterium and semen quality. Overall, it is a well-conducted study that further supports the importance of the seminal microbiota.

Strengths:

- The authors performed the analysis on 223 samples, which is the largest dataset in semen microbiota analysis so far

- Inclusion of negative controls to control contaminations.

- Inclusion of a positive control group consisting of men with proven fertility.

[Editors' note: the authors addressed the concerns raised in the previous round of review.]

Author response:

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

Discussion: Could the authors discuss more the findings about Flavobacterium? Has it ever been associated with the urogenital tract?

Page 13-14, line 252-268:

‘The genus Flavobacterium was defined in 1923 to encompass gram-negative, non-spore-forming rods, of yellow pigment (44). The inclusiveness of this definition resulted in a collective of heterogenous species. By 1984 the genus had been restricted to those that were also non-motile and non-gliding (44). More recently, with an increase in genomic profiling, many species previously considered to be of genus Flavobacterium have been reclassified to genus Chryseobacterium, Cytophaga, and Weeksella (45). Increasing numbers of Flavobacterium species are being discovered such as gondwanense, Collinsii, branchiarum, branchiicola, salegens and scophthalmum (46) (47) (48). The allocation of Flavobacterium aquatile to this genus remains controversial due to its motility (49). Flavobacterium species are widely distributed in the environment including soil, fresh water and saltwater habitats (50) (51).  There are many reports of pathogenic infections of Flavobacterium species in fish, however human infections are rare (48).  A handful of case reports have described opportunistic infections to include pneumonia, urinary tract infection, peritonitis and meningitis (52) (53) (54) (55). Flavobacterium lindanitolerans and Flavobacterium ceti have been isolated as causative agents in some (56) (54). Case reports also describe Flavobacterium odoratum as a causative agent in urinary tract infection, most often in the immunocompromised or those with indwelling devices (57) (58) (59). However, this was one of many species previously of genus Flavobacterium reclassified, in this case to genus Myroides (60). Notably in our sample participants were asymptomatic of urinary tract infection’. 

What is the relative abundance of Flavobacterium in the present study: this type of bacterium has been previously associated with contaminations (PMID: 25387460, 30497919).

Page 13, line 244-247:

‘The Flavobacterium genus taxon we identified as significantly associated with abnormal semen quality and sperm morphology was present in 36.28% of the samples, with a mean relative abundance of 1.15% in those samples. This information and the mention of previous findings of Flavibacterium in contamination studies have been added to the discussion’.

Figure 1: Increase the size of panel A.

Amended.

Figure 3: Can the authors indicate the relative abundance of each genus/species by the size of the node?

Co-occurrence network figure has been modified to display relative abundance of nodes.

Supplementary data: I don't see anywhere the decontam plots.

Decontam plots as suggested in the package vignette https://benjjneb.github.io/decontam/vignettes/decontam_intro.html have been added in the GitHub repository. For practical purposes, the plot corresponding to the frequency testing only display a random subset (n=15) of the total taxa (n=82) flagged by this test as contaminants. The. .csv files with the outputs of each filter are available in the same directory

Line 12: Check the sentence

Line 15: Genera in italics

Line 33: Change "overall quality of the spermatozoa" to "overall semen quality"

Lines 18-20: Rephrase

Line 87: 28F-Borrelia

Line 134: "Seminal microbiota" or "Composition of the seminal microbiota"

Line 159: "These included ... genera"

Line 166: "Of note, Flavobacterium genus was..."

Lines 187-188: Check sentence

Thank you, these have been amended

eLife Assessment

This compelling study introduces a set of novel genetically encoded tools for the selective and reversible ablation of excitatory and inhibitory synapses. These new tools enable selective and efficient ablation of excitatory synapses, and photoactivatable and chemically inducible methods for inhibitory synapse ablation in specific cell types, providing valuable methods for disrupting neural circuits. This approach holds broad potential for investigating the roles of specific synaptic input onto genetically determined cells.

Reviewer #1 (Public review):

Summary:

This work is a continuation of a previous paper from the Arnold group, where they engineered GFE3, which allows to specifically ablate inhibitory synapses. Here, the authors generate 3 different actuators:

(1) An excitatory synapse ablator.<br /> (2) A photoactivatable inhibitory synapse ablator.<br /> (3) A chemically inhibitory synapse ablator.

Following initial engineering, the authors present characterization and optimization data to showcase that these new tools allow one to specifically ablate synapses, without toxicity and with specificity. Furthermore, they showcase that these manipulations are reversible.

Altogether, these new tools would be important for the neuroscience community.

Strengths:

The authors convincingly demonstrate the engineering, optimization and characterization of these new probes. The main novelty here is the new excitatory synapse ablator, which has not been shown yet and thus could be a valuable tool for neuroscientists.

Weaknesses:

The authors have convincingly demonstrated the use of these tools in cultured neurons. The biggest weakness is the limited information given for the use of these tools for in vivo studies. The authors provide one example of the use of these new tool to study retinal circuits, and show evidence that the excitatory synapse ablator reduces synaptic transmission in retinal slices. Still, more work will be required to use this tool in intact neuronal circuits. It remains unclear if it would be trivial to characterize how well these tools express and operate in vivo. This could be substantially different and present some limitations as to the utility of these tools.

Reviewer #2 (Public review):

Summary:

This study introduces a set of genetically encoded tools for the selective and reversible ablation of excitatory and inhibitory synapses. Previously, the authors developed GFE3, a tool that efficiently ablates inhibitory synapses by targeting an E3 ligase to the inhibitory scaffolding protein Gephyrin via GPHN.FingR, a recombinant, antibody-like protein (Gross et al., 2016). Building on this work, they now present three new ablation tools: PFE3, which targets excitatory synapses, and two new versions of GFE3-paGFE3 and chGFE3-that are photoactivatable and chemically inducible, respectively. These tools enable selective and efficient synapse ablation in specific cell types, providing valuable methods for disrupting neural circuits. This approach holds broad potential for investigating the roles of specific synaptic input onto genetically determined cells.

Strengths:

The primary strength of this study lies in the rational design and robust validation of each tool's effectiveness, building on previous work by the authors' group (Gross et al., 2016). Each tool serves distinct research needs: PFE3 enables efficient degradation of PSD-95 at excitatory synapses, while paGFE3 and chGFE3 allow for targeted degradation of Gephyrin, offering spatiotemporal control over inhibitory synapses via light or chemical activation. These tools are efficiently validated through robust experiments demonstrating reductions in synaptic markers (PSD-95 and Gephyrin) and confirming reversibility, which is crucial for transient ablation. By providing tools with both optogenetic and chemical control options, this study broadens the applicability of synapse manipulation across varied experimental conditions, enhancing the utility of E3 ligase-based approaches for synapse ablation.

Weaknesses:

While this study provides valuable tools and addresses many critical points for varidation, examining potential issues with specificity and background ubiquitination in further detail could strengthen the paper. For PFE3, the study demonstrates reductions in both PSD-95 and GluA1. In their previous work, GFE3 selectively reduced Gephyrin without affecting major Gephyrin interactors or other PSD proteins. Clarifying whether PFE3 affects additional PSD proteins beyond GluA1 would be important for accurately interpreting results in experiments using PFE3. Additionally, further insight into PFE3's impact on inhibitory synapses would be valuable to assess the excitatory specificity and potential for circuit-level applications. For paGFE3 and chGFE3, the E3 ligase (RING domain of Mdm2) is overexpressed and thus freely diffusible within the cell as a separate construct. Although the authors show that Gephyrin is not significantly reduced without light or chemical activation, it remains possible that other proteins, particularly non-synaptic proteins, could be ubiquitinated due to the presence of freely diffusing E3 ligase in cytosol. Addressing these points would clarify the strengths and limitations of tools, providing users with valuable information.

Author response:

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

Public Reviews

Reviewer #1:

The biggest concern in this regard is: that almost all the characterization is performed in cultured dissociated neurons…

While it is true that most of the characterization done in this paper was in cultured neurons, we verified that PFE3 mediates functional ablation of excitatory synapses in vivo (Fig. 3). Furthermore, the GPHN.FingR-XIAP (GFE3), a protein very similar to the complex formed following activation of paGFE3 and chGFE3, has been extensively tested by us and others in vivo(1-4).

Reviewer #2:

For paGFE3 and chGFE3, the E3 ligase (RING domain of Mdm2) is overexpressed throughout cells as a separate construct. Although the authors show that Gephyrin is not significantly reduced without light or chemical activation, it remains possible that other proteins could be ubiquitinated due to the overexpressed E3 domain.

In our previous paper(1), we tested neurons under 3 conditions: 1. expressing a construct similar to PBP-E3, consisting of a FingR with a randomized binding domain fused to the same XIAP ring domain used in paGFE3 and chGFE3 (RAND-E3). 2. expressing GPHN.FingR. 3. not expressing any exogenous proteins (control neurons). In each case, we found that expression of a variety of excitatory and inhibitory synaptic proteins was not significantly different when exposed to either of these exogenous proteins compared with control neurons.

Recommendations for the authors:

(1)  Can the authors use the tools to show the ablation of endogenous PSD95 without FingR overexpression?

The experiments described in Fig. 3 are an example of this type of experiment. Furthermore, the PSD-95.FingR was extensively tested and has been used in dozens of studies without any indication that its expression alters cellular function or morphology. Note also that the transcriptional regulation system of PSD-95.FingR limits the expression such that there is virtually no background, so it is not really being overexpressed.

(2) I am missing some control experiments for the excitatory synapses ablator- can the authors show that cells transfected with the plasmid and no DOX, show similar numbers of synapses as neurons without transfection?

We have added an experiment comparing cells expressing PSD-95.FingR alone, and others expressing PFE3 with no Dox. We found that the two types of cells express amounts of PSD-95 that are not significantly different (Fig. S2L).

(3) I am not quite sure how they used paired statistics on staining since they could only stain the cell at the end of the experiment. Are the comparisons performed on different cells?

These experiments were done on the same cells. However, the methods of labeling were different- the initial counting of synapses was done, so we agree with the reviewer that it would be best not to use a paired analysis. Accordingly, we have changed Figs. 1F and 2D.

eLife Assessment

The paper describes a novel approach for inferring features of synaptic networks from recordings of individual cells within the network. The paper will be a valuable contribution to those studying central pattern generators, including those involved in respiration. However, the theoretical approach to drawing inferences regarding the underlying synaptic currents is incomplete as it relies on unsupported simplifying assumptions.

Reviewer #1 (Public review):

Summary:

The paper develops a phase method to obtain the excitatory and inhibitory afferents to certain neuron populations in the brainstem. The inferred contributions are then compared to the results of voltage clamp and current clamp experiments measuring the synaptic contributions to post-I, aug-E and ramp-I neurons.

Strengths:

The electrophysiology part of the paper is sound and reports novel features with respect to earlier work by JC Smith et al 2012, Paton et al 2022 (and others) who have mapped circuits of the respiratory central pattern generator. Measurements on ramp-I neurons, late-I neurons and two types of post-I neurons in Fig.2 besides measurements of synaptic inputs to these neurons in Fig.5 are to my knowledge new.

Weaknesses:

The phase method for inferring synaptic conductances fails to convince. The method rests on many layers of assumptions and the inferred connections in Fig.4 remain speculative. To be convincing, such method ought to be tested first on a model CPG with known connectivity to assess how good it is at inferring known connections back from the analysis of spatio-temporal oscillations. For biological data, once the network connectivity has been inferred as claimed, the straightforward validation is to reconstruct the experimental oscillations (Fig.2) noting that Rybak et al (Rybak, Paton Schwaber J. Neurophysiol. 77, 1994 (1997)) have already derived models for the respiratory neurons.

The transformation from time to phase space, unlike in the Kuramoto model, is not justified here (L.94) and is wrong. The underpinning idea that "the synaptic conductances depend on the cycle phase and not on time explicitly" is flawed because synapses have characteristic decay times and delays to response which remain fixed when the period of network oscillations increases. Synaptic properties depend on time and not on phase in the network. One major consequence relevant to the present identification of excitatory or inhibitory behaviour, is that it cannot account for change in behaviour of inhibitory synapses - from inhibitory to excitatory action - when the inhibitory decay time becomes commensurable to the period of network oscillations (Wang & Buzsaki Journal of Neuroscience 16, 6402 (1996), van Vreeswijk et al. J. Comp. Neuroscience 1,313 (1994), Borgers and Kopell Neural Comput. 15, 2003). In addition, even small delays in the inhibitory synapse response relative to the pre-synaptic action potential also produce in-phase synchronization (Chauhan et al., Sci. Rep. 8, 11431 (2018); Borgers and Kopell, Neural Comput. 15, 509 (2003)). The present assumption are way too simplistic because you cannot account for these commensurability effects with a single parameter like the network phase. There is therefore little confidence that this model can reliably distinguish excitatory from inhibitory synapses when their dynamics properties are not properly taken into account.

L..82, Eq.1 makes extremely crude assumptions that the displacement current (CdV/dt) is negligible and that the ion channel currents are all negligible. Vm(t) is also not defined. The assumption that the activation/inactivation times of all ion channels are small compared to the 10-20ms decay time of synaptic currents is not true in general. Same for the displacement current. The leak conductance is typically g~0.05-0.09ms/cm^2 while C~1uF/cm^2. Therefore the ratio C/g leak is in the 10-20ms range - the same as the typical docking neurotransmitter time in synapses.

Models of brainstem CPG circuits have been known to exist for decades: JC Smith et al 2012, Paton et al 2022, Bellingham Clin. Exp. Pharm. And Physiol. 25, 847 (1998); Rubin et al., J. Neurophysiol. 101, 2146 (2009) among others. The present paper does not discuss existing knowledge on respiratory networks and gives the impression of reinventing the wheel from scratch. How will this paper add to existing knowledge?

Comments on revisions:

The authors have done a good job at revising the manuscript to put this work into the context of earlier work on brainstem central pattern generators.

I still believe the case for the method is not as convincing as it would have been if the method had been validated first on oscillations produced by a known CPG model. Why would the inference of synaptic types from the model CPG voltage oscillations be predetermined? Such inverse problems are quite complicated and their solution is often not unique or sufficiently constrained. Recovering synaptic weights (or CPG parameters) from limited observations of a highly nonlinear system is not warranted (Gutenkunst et al., Universally sloppy parameter sensitivities in systems biology models, PLoS Comp. Biol. 2007; www.doi.org/10.1371/journal.pcbi.0030189) especially when using surrogate biological models like Hodgkin-Huxley models.

In p.2, the edited section refers to the interspike interval being much smaller than the period of the network. More important is to mention the relationship between the decay time of inhibitory synapses and the period of the network.

Reviewer #2 (Public review):

Summary:

By measuring intracellular changes in membrane voltage from a single neuron of the medulla the authors describe a method for determining the balance of excitatory and inhibitory synaptic drive onto a single neuron within this important brain region.

Strengths:

This data-driven approach to exploring neural circuits is well described and could be valuable in identifying microcircuits that generate rhythms. Importantly, perhaps, this inference method could enable microcircuits to be studied without the need for time consuming anatomical tracing or other more involved electrophysiological techniques. Therefore, I definitely can see the value in developing an approach of this type.

Weaknesses:

There are many assumptions that need to be accepted in order to successfully apply this technique and I was pleased to see that several of these assumption have been explored by the authors in this study.

For example, this approach involves assuming the reversal potential that is associated with the different permeant ions that underlie the excitation and inhibition as well as the application of Ohms law to estimate the contribution of excitation and inhibitory conductance. My first concern was that this approach relies on a linear I-V relationship between the measured voltage and the estimated reversal potential. However, open rectification is a feature of any I-V relationship generated by asymmetric distributions of ions (see the GHK current equation) and will therefore be a particular issue for the inhibition resulting from asymmetrical Cl- ion gradients across GABA-A receptors. The mixed cation conductance that underlies most synaptic excitation will also generate a non-linear I-V relationship due to the inward rectification associated with polyamine block of AMPA receptors. The authors present evidence that over most of the voltage range examined the I-V relationship is linear and this is a helpful addition.

This approach has similarities to earlier studies undertaken in the visual cortex that estimated the excitatory and inhibitory synaptic conductance changes that contributed to membrane voltage changes during receptive field stimulation. However, these approaches also involved the recording of transmembrane current changes during visual stimulation that were undertaken in voltage-clamp at various command voltages to estimate the underlying conductance changes. Molkov et al have attempted to essentially deconvolve the underlying conductance changes without this information and I am concerned that this simply may not be possible.

The current balance equation (1) cited in this study is based upon the parallel conductance model developed by Hodgkin & Huxley. One key element of the HH equations is the inclusion of an estimate of the capacitive current generated due to the change in voltage across the membrane capacitance. While the present study takes into account the impact of membrane capacitance, a deeper discussion on how variations in capacitance across different neuron types might affect inference accuracy would be useful. Differences in capacitance could introduce variability in inferred conductances, potentially influencing model predictions.

Studies using acute slicing preparations to examine circuit effects have often been limited to the study of small microcircuits - especially feedforward and feedback interneuron circuits. It is widely accepted that any information gained from this approach will always be compromised by the absence of patterned afferent input from outside the brain region being studied. In this study, descending control from the Pons and the neocortex will not be contributing much to the synaptic drive and ascending information from respiratory muscles will also be absent completely. This may not have been such a major concern if this study was limited to demonstrating the feasibility of a methodological approach. However, this limitation does need to be considered when using an approach of this type to speculate on the prevalence of specific circuit motifs within the medulla (Figure 4). Therefore, I would argue that some discussion of this limitation should be included in this manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The paper develops a phase method to obtain the excitatory and inhibitory afferents to certain neuron populations in the brainstem. The inferred contributions are then compared to the results of voltage clamp and current clamp experiments measuring the synaptic contributions to post-I, aug-E, and ramp-I neurons.

Strengths:

The electrophysiology part of the paper is sound and reports novel features with respect to earlier work by JC Smith et al 2012, Paton et al 2022 (and others) who have mapped circuits of the respiratory central pattern generator. Measurements on ramp-I neurons, late-I neurons, and two types of post-I neurons in Figure 2 besides measurements of synaptic inputs to these neurons in Figure 5 are to my knowledge new.

Weaknesses:

The phase method for inferring synaptic conductances fails to convince. The method rests on many layers of assumptions and the inferred connections in Figure 4 remain speculative. 

We hope that the additional method justifications now incorporated in the manuscript will make our method more convincing and change this reviewer’s opinion.

To be convincing, such a method ought to be tested first on a model CPG with known connectivity to assess how good it is at inferring known connections back from the analysis of spatio-temporal oscillations. 

We respectfully disagree with this critique. Existing respiratory CPG models are based on a conductance-based formalism. Since the neurons recorded using our approach are typically hyperpolarized, in the model at the corresponding values of the membrane potential, all voltage-gated channels will be deactivated. Therefore, the current balance equation used in this study will closely align with the descriptions used in these models. This alignment will result in a near-exact correspondence between the synaptic conductance values inferred by our method and their model counterparts. However, we believe that such a demonstration, while predetermined to be successful, would not be convincing for a computationally savvy audience.

For biological data, once the network connectivity has been inferred as claimed, the straightforward validation is to reconstruct the experimental oscillations (Figure 2) noting that Rybak et al (Rybak, Paton Schwaber J. Neurophysiol. 77, 1994 (1997)) have already derived models for the respiratory neurons.

Running such simulations is beyond the scope of this paper, which focuses on our methods for extracting synaptic conductances during network activity cycles from intracellular recordings. However, the existing, largely speculative, respiratory CPG models can be validated against the "ground truth" of the inferences we present here. To illustrate how our circuit connection motifs elaborate on existing respiratory CPG models, we have now included a combinatorial connectivity model in the manuscript derived from the connectivity motifs in the supplemental figures (Figure 4 Supplemental Figure 1) with comparisons to the model schematic utilized by Rybak, Smith et al. in simulation studies to simulate a rhythmic three-phase respiratory pattern. There are conserved mechanistically important connectivity features between these schematics that it is possible to suggest that our more elaborate connectivity scheme would almost certainly generate the three-phase patterns of neuronal firing and network rhythmic activity.

The transformation from time to phase space, unlike in the Kuramoto model, is not justified here (Line 94) and is wrong. The underpinning idea that "the synaptic conductances depend on the cycle phase and not on time explicitly" is flawed because synapses have characteristic decay times and delays to response which remain fixed when the period of network oscillations increases. Synaptic properties depend on time and not on phase in the network. 

The primary assumption of our method is that all variables within the system are periodic functions of time. Therefore, the inputs to the recorded neuron, at minimum, are fully defined by the oscillation's phase. While the transduction of the input into postsynaptic conductance may have its own time dependence, the characteristic timescale of synaptic dynamics (10-20 ms, as suggested by the reviewer) is much smaller than the period of network oscillations. This is certainly true for the test system we are using. This valid assumption of our method is now further clarified in the revised manuscript.

One major consequence relevant to the present identification of excitatory or inhibitory behaviour, is that it cannot account for change in the behaviour of inhibitory synapses - from inhibitory to excitatory action - when the inhibitory decay time becomes commensurable to the period of network oscillations (Wang & Buzsaki Journal of Neuroscience 16, 6402 (1996), van Vreeswijk et al. J. Comp. Neuroscience 1,313 (1994), Borgers and Kopell Neural Comput. 15, 2003). 

Our method focuses on recovering synaptic conductances rather than directly measuring presynaptic inputs. The conversion of presynaptic inputs (spike trains) into postsynaptic conductances involves its own time scales. This can lead to complex dynamical effects when synaptic delay or decay times are comparable to the oscillation period. In such cases, although our conductance calculation remains accurate, we might misinterpret the phase of the presynaptic input, as it may not align with the phase of the postsynaptic conductance peak. However, this discrepancy is not significant for applications where the synaptic delay/decay times are considerably shorter than the oscillation period.

In addition, even small delays in the inhibitory synapse response relative to the pre-synaptic action potential also produce in-phase synchronization (Chauhan et al., Sci. Rep. 8, 11431 (2018); Borgers and Kopell, Neural Comput. 15, 509 (2003)). 

The reviewer is referring to a phenomenon involving interspike synchronization that generates oscillations with very short periods, comparable to synaptic delay times. Our technique, in contrast, is designed for systems of asynchronously firing neurons forming functional populations whose oscillations emerge on a much longer time scale or are driven by periodic stimuli (e.g., sensory input) with a period much longer than the interspike intervals of individual neurons. The time scale difference we are addressing in our test system is two orders of magnitude.

The present assumptions are way too simplistic because you cannot account for these commensurability effects with a single parameter like the network phase. There is therefore little confidence that this model can reliably distinguish excitatory from inhibitory synapses when their dynamic properties are not properly taken into account.

As we explained in our previous responses, in our test system, we can reliably resolve post-synaptic conductance variations at 1/100th of the oscillation period. This is due to a >100X time scale difference between the oscillation period and the synaptic/membrane decay time constants. The efficiency of our method in other systems may vary depending on the relationship between the membrane time constant and the oscillation period. The text now provides a clearer discussion of the method's resolution.

To interpret post-synaptic conductance profiles in terms of presynaptic inputs (e.g., to reconstruct connectivity), one should consider the input-to-conductance transduction processes.We did not aim to provide a general solution for this step in our paper (hence the title) as these processes may differ for different neurotransmitter systems and involve individual dynamics. However, in our test system, as discussed, the oscillation period is much longer than the synaptic decay times of the fast-acting neurotransmitters involved (i.e., glutamate, glycine, and GABA). This means that the possible phase difference between presynaptic neuronal activity and the corresponding postsynaptic conductances is negligible. This allows for a straightforward interpretation of conductance profiles in terms of the functional connectivity of the network. In other systems, the situation may, of course, be different and additional efforts for inferring the presynaptic activity from postsynaptic conductance profiles may be necessary.

Line 82, Equation 1 makes extremely crude assumptions that the displacement current (CdV/dt) is negligible and that the ion channel currents are all negligible. Vm(t) is also not defined. The assumption that the activation/inactivation times of all ion channels are small compared to the 10-20ms decay time of synaptic currents is not true in general. Same for the displacement current. The leak conductance is typically g~0.05-0.09ms/cm^2 while C~1uF/cm^2. Therefore the ratio C/g leak is in the 10-20ms range - the same as the typical docking neurotransmitter time in synapses.

We have explicitly included capacitive current in the model formulation and described the time scale separation requirement that justifies our approach. Additionally, we now explain within the text that the current injection protocol involves hyperpolarizing the recorded neuron to ensure voltage-dependent currents remain deactivated during the recording. The remarkable linearity of the current-voltage relationships observed in the vast majority of recorded neurons provides post-hoc evidence supporting this assumption. For further details, please refer to our responses to Reviewer 2 and Figure 1 Supplemental Figure 1 as an example.

Models of brainstem CPG circuits have been known to exist for decades: JC Smith et al 2012, Paton et al 2022, Bellingham Clin. Exp. Pharm. And Physiol. 25, 847 (1998); Rubin et al., J. Neurophysiol. 101, 2146 (2009) among others. The present paper does not discuss existing knowledge on respiratory networks and gives the impression of reinventing the wheel from scratch. How will this paper add to existing knowledge?

We appreciate this comment, and in fact, in the original submitted version of this manuscript, we discussed existing knowledge of respiratory networks, but there was editorial concern that this material was above and beyond the technical aspects that we were trying to convey and therefore may detract from the paper as a technical submission. To strike a balance, we have re-incorporated some of this material in abbreviated form into the Discussion section “Implications of reconstructed synaptic conductance profiles for respiratory functional circuit architecture”.

Reviewer #2 (Public review):

Summary:

By measuring intracellular changes in membrane voltage from a single neuron of the medulla the authors describe a method for determining the balance of excitatory and inhibitory synaptic drive onto a single neuron within this important brain region.

Strengths:

This approach could be valuable in describing the microcircuits that generate rhythms within this respiratory control centre. This method could more generally be used to enable microcircuits to be studied without the need for time-consuming anatomical tracing or other more involved electrophysiological techniques.

Weaknesses:

This approach involves assuming the reversal potential that is associated with the different permeant ions that underlie the excitation and inhibition as well as the application of Ohms law to estimate the contribution of excitation and inhibitory conductance. My first concern is that this approach relies on a linear I-V relationship between the measured voltage and the estimated reversal potential. However, open rectification is a feature of any I-V relationship generated by asymmetric distributions of ions (see the GHK current equation) and will therefore be a particular issue for the inhibition resulting from asymmetrical Cl- ion gradients across GABA-A receptors. The mixed cation conductance that underlies most synaptic excitation will also generate a non-linear I-V relationship due to the inward rectification associated with the polyamine block of AMPA receptors. Could the authors please speculate what impact these non-linearities could have on results obtained using their approach?

In our Figure 1 Supplemental Figure 1, we illustrated that I-V relationships for each particular phase of the cycle (except for transitions between inspiration and expiration where our error estimates are greatest) are remarkably linear. 

In Author response iamge 1 we compare the I-V dependence for Cl- as predicted by the GHK equation and its linear approximation using constant conductance and the Cl- Nernst potential. One can see that in the typical range of voltages used (shown by solid black vertical lines), the linear approximation appears quite adequate.

Author response image 1.

This approach has similarities to earlier studies undertaken in the visual cortex that estimated the excitatory and inhibitory synaptic conductance changes that contributed to membrane voltage changes during receptive field stimulation. However, these approaches also involved the recording of transmembrane current changes during visual stimulation that were undertaken in voltage-clamp at various command voltages to estimate the underlying conductance changes. Molkov et al have attempted to essentially deconvolve the underlying conductance changes without this information and I am concerned that this simply may not be possible. 

This was why we compared the results of our reconstructions applied to current- and voltage-clamp recordings from the same neurons and we found, as illustrated, that the synaptic conductance profiles are qualitatively identical with both techniques.

The current balance equation (1) cited in this study is based on the parallel conductance model developed by Hodgkin & Huxley. However, one key element of the HH equations is the inclusion of an estimate of the capacitive current generated due to the change in voltage across the membrane capacitance. I would always consider this to be the most important motivation for the development of the voltage-clamp technique in the 1930's. Indeed, without subtraction of the membrane capacitance, it is not possible to isolate the transmembrane current in the way that previous studies have done. In the current study, I feel it is important that the voltage change due to capacitive currents is taken into consideration in some way before the contribution of the underlying conductance changes are inferred.

We have incorporated the capacitive current into the initial model formulation and established explicit requirements for time scale separation. These requirements justify the application of our method. Specifically, the membrane time constant (C/g ~ 10ms in our test system) must be substantially shorter than the period of network oscillations (T ~ 2s in our test system). Under this condition, aggregate variations in synaptic conductances can be considered slow, allowing us to treat membrane voltage as being in instantaneous equilibrium. This defines the time resolution of our method. Please refer to our responses to Reviewer 1 and the revised manuscript text for a more detailed explanation.

Studies using acute slicing preparations to examine circuit effects have often been limited to the study of small microcircuits - especially feedforward and feedback interneuron circuits. It is widely accepted that any information gained from this approach will always be compromised by the absence of patterned afferent input from outside the brain region being studied. In this study, descending control from the Pons and the neocortex will not be contributing much to the synaptic drive and ascending information from respiratory muscles will also be absent completely. This may not have been such a major concern if this study was limited to demonstrating the feasibility of a methodological approach. However, this limitation does need to be considered when using an approach of this type to speculate on the prevalence of specific circuit motifs within the medulla (Figure 4). Therefore, I would argue that some discussion of this limitation should be included in this manuscript.

Our experimental brainstem-spinal cord in situ preparation does include important inputs from the pons that are necessary to generate the 3-phase respiratory pattern (e.g., Smith et al. (2013). Brainstem respiratory networks: building blocks and microcircuits. Trends Neurosci, 36(3), 152-162), but we agree that other inputs such as from midbrain and cortex as well as important peripheral afferents are absent, and we have now noted this limitation in the text at the end of the new section “Implications of reconstructed synaptic conductance profiles for respiratory functional circuit architecture“. We show specific circuit motifs simply to illustrate how our readout of synaptic conductances from single neurons and the information on the main neuronal activity patterns in our experimental preparation can be interpreted. We thought that it would be useful to illustrate and interpret inferred connectivity motifs as an output of our methodological approach. As we now discuss in the section “Implications of reconstructed synaptic conductance profiles for respiratory functional circuit architecture” in response to Reviewer #1, our circuit motifs are consistent with some sets of connections that have been speculated in the literature, but they also provide some novel information about connectivity that we have been able to infer for respiratory circuits from the complex sets of synaptic conductances indicated by our approach. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major comments:

(1) My recommendation is to clarify how each neuron population was identified. Individual populations are very hard to identify based on morphology alone in brain slices such as Supplemental Figure 1. I assume the authors identified each population based on their phase difference relative to the inspiratory pulse in the phrenic nerve. This ought to be clarified. 

Neuronal populations were classified based on their firing patterns within the respiratory cycle. Immunohistochemistry was only used for post-hoc identification of the transmitter phenotype in select neurons. Specifically, recorded neurons were categorized according to the phase range of the respiratory cycle in which they fired and their firing pattern during that range. For example, neurons firing during inspiration (synchronously with the phrenic nerve) with a progressively increasing firing rate were classified as ramp-I, etc., as illustrated in the figure depicting phase-dependent firing patterns. This classification is detailed in the "Firing patterns of respiratory interneurons" sub-section.

It would also be beneficial to discuss the benefits and limitations of using this preparation relative to brainstem slices and in-vivo preparations (e.g. Moraes et al. J. Physiol. 599, 3237 (2021)) for measuring live network activity.

We provided the reference to an important recent review (Paton et al. 2022, Advancing respiratory-cardiovascular physiology with the working heart-brainstem preparation over 25 years. J Physiol, 600(9), 2049-2075) on the benefits and limitations of using the in situ rodent brainstem-spinal cord preparation employed in our study. 

(2) The background on inference methods is similarly thin. The works in line 47 are mainly experimental characterizations of excitatory and inhibitory cells. Techniques for estimating network conductances/parameters ought to be covered. One reference that comes to mind: Armstrong, E. Statistical data assimilation for estimating electrophysiology simultaneously with connectivity within a biological neuronal network. Physical Review E 101, 012415, 2020.

Our technique is not intended to estimate synaptic connections between neurons from paired recordings. Instead, we calculate the dynamics of inhibitory and excitatory synaptic conductances that result from many concurrent synaptic inputs representing aggregate activities of the functionally interacting populations. The previous studies that we cited are the ones that have direct or indirect relation to this paradigm. 

(3) How the "patterns of synaptic conductances" in phase diagrams imply the network connectivity (l.244) is not clear. Are the patterns of "activity patterns" depicted in Figure 2 the only neuron populations driving the postsynaptic neurons in Figure 4? 

Figure 2 shows all of the basic firing patterns that we have recorded in our experimental preparation. So, yes, assuming that all periodic inputs in this network originate from within the network, those 6 populations are the main sources of the corresponding patterns.

The methodology for constructing the networks is unclear, 

This is explained in detail in the section "Synaptic Conductances and Functional Connectome of Respiratory Interneurons". Specifically, when a neuron with a given firing pattern (and thus belonging to a corresponding population, e.g., pre-I/I) exhibits excitatory or inhibitory conductance during a particular phase of the respiratory cycle (e.g., inhibition during the first half of expiration, as in Figure 3A1), we infer that the population with the same firing pattern receives input from a population with an activity pattern matching the postsynaptic conductance profile (e.g., the pre-I/I population receives post-I inhibition, as in Figure 4A1).

yet 6 lines later (l.251) the narrative jumps to the conclusion that "the information on inhibitory transmitter phenotypes...indeed corroborates that subsets of the presynaptic neurons are inhibitory" and further "conductance profiles, which gives additional confidence in the correlation between pre-synaptic firing patterns and likely post-synaptic interactions". The method also blends in empirical information from immune labelling. It is unclear what method can actually infer on its own.

The functional connections that we were able to infer implied that neurons with specific firing patterns (e.g., post-I neurons) must include neurons with specific transmitter phenotypes (e.g., inhibitory). Immune labeling results were used to show that there are indeed neurons having corresponding firing patterns and neurotransmitter phenotypes. It has nothing to do with the inference method. It just shows that our assumption about various inhibitory inputs originating from within the network is plausible.

(4) Figure 3 - why does the Early-I population which is connected by the same mutually inhibitory links as Post-I and Aug-E within the respiratory CPG have the opposite conductance activation sequence as post-I and aug-E. Namely, it receives excitatory input at phases 0,1,2 when post-I and aug-E receive inhibitory input?

We added the section “Implications of reconstructed synaptic conductance profiles for respiratory functional circuit architecture” discussing the correspondence and inconsistencies between our findings and existing respiratory CPG models (see Figure 4 Supplemenntal Figure 1). For this specific question, phase 0, 1 and 2 represent the same phase of the respiratory cycle corresponding to a transition from expiration to inspiration. According to the Rybak et al. models, the early-I population receives excitation from the pre-I/I population which is active at the E-I transition and throughout the entire inspiratory phase of the cycle. This is largely consistent with our findings shown in Figure 3. Also, according to Rybak et al., post-I and aug-E populations are inhibited by early-I neurons, which is also consistent with inspiratory inhibition in all examples of these neurons that we show in Figure 3. As noted in other responses to the reviewers’ comments, we have now discussed in the “Implications of reconstructed synaptic conductance profiles for respiratory functional circuit architecture” which covers some comparisons to previously inferred connectivity in the respiratory network.

Minor comments:

(1) l.39 - The terminology "patterns of inhibitory and excitatory synaptic conductances" used throughout the manuscript (l.66, 241, 244, 259...) is vague.

We defined this terminology in the updated version.

(2) Figure 1 what is the integration time of the moving median in Figure 1a?

0.1s. Now included in the figure legend.

(3) L.128 "rhythmic inspiratory neuron" which one is this post-I, aug-E, early-I?

This example demonstrates a pre-I/I firing pattern, as the neuron begins firing slightly before the phrenic burst and continues throughout inspiration (as defined by phrenic nerve activity). However, this is merely an arbitrary example used to illustrate the methodology. The actual firing pattern of the recorded neuron is not considered in any way for synaptic conductance inference.

(4) Figure 3 What the panel labelling means A1, B1, A2, etc. is not disclosed in the caption.

These labels are used in the text to refer to specific examples. Now it is explained in the caption that the letter corresponds to the firing phenotype indicated on the top of each column and the digit refers to the example number.

(5) L.129/ L.133 - the diagram of the medulla in Supplementary Figure 1 ought to be inserted early on in the main text when introducing the respiratory CPG, phrenic and vagal signals.

This is a good suggestion and we have linked this figure specifically to Figure 2 as Figure 2 Supplemental Figure 1 in the main text to better orient readers.

(6) L. 457 - Reference needed on reversal potentials.

We report what we observed, so it is unclear what reference the reviewer means.

eLife Assessment

This neuroimaging and electrophysiology study in a small cohort of congenital cataract patients with sight recovery aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in visual cortex. While contrasting sight-recovery with visually intact controls suggested the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, it provided incomplete evidence supporting claims about the effects of early deprivation itself. The reported data were considered valuable, given the rare study population. However, methodological limitations will likely restrict usefulness to scientists working in this particular subfield.

Reviewer #1 (Public review):

Summary

In this human neuroimaging and electrophysiology study, the authors aimed to characterise effects of a period of visual deprivation in the sensitive period on excitatory and inhibitory balance in the visual cortex. They attempted to do so by comparing neurochemistry conditions ('eyes open', 'eyes closed') and resting state, and visually evoked EEG activity between ten congenital cataract patients with recovered sight (CC), and ten age-matched control participants (SC) with normal sight. First, they used magnetic resonance spectroscopy to measure in vivo neurochemistry from two locations, the primary location of interest in the visual cortex, and a control location in the frontal cortex. Such voxels are used to provide a control for the spatial specificity of any effects because the single-voxel MRS method provides a single sampling location. Using MR-visible proxies of excitatory and inhibitory neurotransmission, Glx and GABA+ respectively, the authors report no group effects in GABA+ or Glx, no difference in the functional conditions 'eyes closed' and 'eyes open'. They found an effect of group in the ratio of Glx/GABA+ and no similar effect in the control voxel location. They then perform multiple exploratory correlations between MRS measures and visual acuity and report a weak positive correlation between the 'eyes open' condition and visual acuity in CC participants. The same participants then took part in an EEG experiment. The authors selected two electrodes placed in the visual cortex for analysis and report a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. Control electrodes in the frontal region did not present with the same pattern. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

The authors report the difference in E/I ratio and interpret the lower E/I ratio as representing an adaptation to visual deprivation, which would have initially caused a higher E/I ratio. Although intriguing, the strength of evidence in support of this view is not strong. Amongst the limitations are the low sample size, a critical control cohort that could provide evidence for higher E/I ratio in CC patients without recovered sight for example, and lower data quality in the control voxel. Nevertheless, the study provides a rare and valuable insight into experience-dependent plasticity in the human brain.

Strengths of study

How sensitive period experience shapes the developing brain is an enduring and important question in neuroscience. This question has been particularly difficult to investigate in humans. The authors recruited a small number of sight-recovered participants with bilateral congenital cataracts to investigate the effect of sensitive period deprivation on the balance of excitation and inhibition in the visual brain using measures of brain chemistry and brain electrophysiology. The research is novel, and the paper was interesting and well-written.

Limitations

Low sample size. Ten for CC and ten for SC, and further two SC participants were rejected due to lack of frontal control voxel data. The sample size limits the statistical power of the dataset and increases the likelihood of effect inflation.

In the updated manuscript, the authors have provided justification for their sample size by pointing to prior studies and the inherent difficulties in recruiting individuals with bilateral congenital cataracts. Importantly, this highlights the value the study brings to the field while also acknowledging the need to replicate the effects in a larger cohort.

Lack of specific control cohort. The control cohort has normal vision. The control cohort is not specific enough to distinguish between people with sight loss due to different causes and patients with congenital cataracts with co-morbidities. Further data from a more specific populations, such as patients whose cataracts have not been removed, with developmental cataracts, or congenitally blind participants, would greatly improve the interpretability of the main finding. The lack of a more specific control cohort is a major caveat that limits a conclusive interpretation of the results.

In the updated version, the authors have indicated that future studies can pursue comparisons between congenital cataract participants and cohorts with later sight loss.

MRS data quality differences. Data quality in the control voxel appears worse than in the visual cortex voxel. The frontal cortex MRS spectrum shows far broader linewidth than the visual cortex (Supplementary Figures). Compared to the visual voxel, the frontal cortex voxel has less defined Glx and GABA+ peaks; lower GABA+ and Glx concentrations, lower NAA SNR values; lower NAA concentrations. If the data quality is a lot worse in the FC, then small effects may not be detectable.

In the updated version, the authors have added more information that informs the reader of the MRS quality differences between voxel locations. This increases the transparency of their reporting and enhances the assessment of the results.

Because of the direction of the difference in E/I, the authors interpret their findings as representing signatures of sight improvement after surgery without further evidence, either within the study or from the literature. However, the literature suggests that plasticity and visual deprivation drives the E/I index up rather than down. Decreasing GABA+ is thought to facilitate experience dependent remodelling. What evidence is there that cortical inhibition increases in response to a visual cortex that is over-sensitised to due congenital cataracts? Without further experimental or literature support this interpretation remains very speculative.

The updated manuscript contains key reference from non-human work to justify their interpretation.

Heterogeneity in patient group. Congenital cataract (CC) patients experienced a variety of duration of visual impairment and were of different ages. They presented with co-morbidities (absorbed lens, strabismus, nystagmus). Strabismus has been associated with abnormalities in GABAergic inhibition in the visual cortex. The possible interactions with residual vision and confounds of co-morbidities are not experimentally controlled for in the correlations, and not discussed.

The updated document has addressed this caveat.

Multiple exploratory correlations were performed to relate MRS measures to visual acuity (shown in Supplementary Materials), and only specific ones shown in the main document. The authors describe the analysis as exploratory in the 'Methods' section. Furthermore, the correlation between visual acuity and E/I metric is weak, not corrected for multiple comparisons. The results should be presented as preliminary, as no strong conclusions can be made from them. They can provide a hypothesis to test in a future study.

This has now been done throughout the document and increases the transparency of the reporting.

P.16 Given the correlation of the aperiodic intercept with age ("Age negatively correlated with the aperiodic intercept across CC and SC individuals, that is, a flattening of the intercept was observed with age"), age needs to be controlled for in the correlation between neurochemistry and the aperiodic intercept. Glx has also been shown to negatively correlates with age.

This caveat has been addressed in the revised manuscript.

Multiple exploratory correlations were performed to relate MRS to EEG measures (shown in Supplementary Materials), and only specific ones shown in the main document. Given the multiple measures from the MRS, the correlations with the EEG measures were exploratory, as stated in the text, p.16, and in Fig.4. yet the introduction said that there was a prior hypothesis "We further hypothesized that neurotransmitter changes would relate to changes in the slope and intercept of the EEG aperiodic activity in the same subjects." It would be great if the text could be revised for consistency and the analysis described as exploratory.

This has been done throughout the document and increases the transparency of the reporting.

The analysis for the EEG needs to take more advantage of the available data. As far as I understand, only two electrodes were used, yet far more were available as seen in their previous study (Ossandon et al., 2023). The spatial specificity is not established. The authors could use the frontal cortex electrode (FP1, FP2) signals as a control for spatial specificity in the group effects, or even better, all available electrodes and correct for multiple comparisons. Furthermore, they could use the aperiodic intercept vs Glx in SC to evaluate the specificity of the correlation to CC.

This caveat has been addressed. The authors have added frontal electrodes to their analysis, providing an essential regional control for the visual cortex location.

Comments on revisions:

In the first revision, the authors made reasonable adjustments to their manuscript that addressed most of my comments by adding further justification for their methodology, essential literature support, pointing out exploratory analyses, limitations and adding key control analyses. Their revised manuscript was overall improved, providing valuable information, though the evidence that supports their claims is still incomplete.

In their second revision, the authors pointed to justifications for their analyses, careful interpretation and tempered claims to clarify their response to the initial feedback. However, my assessment of the first revision has not been changed after the second revision, because there were no further modifications of their responses to my feedback.

Reviewer #2 (Public review):

Summary:

The study examined 10 congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts, measuring neural activity and neuro chemical profiles from the visual cortex. The declared aim is to test whether restoring visual function after years of complete blindness impacts excitation/inhibition balance in the visual cortex. The manuscript reports precious behavioural, electrophysiological and magnetic resonance data from a rare population. Although the findings are useful for stimulating further research in the field, they only provide incomplete support to the authors' claims.

The main claim is that sight recovery impacts the excitation/inhibition balance in the visual cortex; however, the paradigm does not allow to distinguish the effects of sight recovery from those of visual deprivation (i.e. in patients who were born blind but recovered vision after several months/years vs. patients who were born blind and never recovered vision); moreover, the link between electrophysiological findings and cortical excitation/inhibition is tentative and its interpretation remains speculative.

Strengths:

The findings are undoubtedly useful for the community, as they contribute towards characterising the many ways in which this special population differs from normally sighted individuals. The combination of MRS and EEG measures is a promising strategy to estimate a fundamental physiological parameter - the balance between excitation and inhibition in the visual cortex, which animal studies show to be heavily dependent upon early visual experience. Thus, the reported results pave the way for further studies, which may use a similar approach to evaluate more patients and control groups.

Weaknesses:

The main methodological limitation is the lack of an appropriate comparison group or condition to delineate the effect of sight recovery (as opposed to the effect of congenital blindness). Few previous studies suggested that Excitation/Inhibition ratio in the visual cortex is increased in congenitally blind patients; the present study reports that E/I ratio decreases instead. The authors claim that this implies a change of E/I ratio following sight recovery. However, supporting this claim would require showing a shift of E/I after vs. before the sight-recovery surgery, or at least it would require comparing patients who did and did not undergo the sight-recovery surgery (as common in the field).

There are also more technical limitations related to the correlation analyses, which are partly acknowledged in the manuscript. A bland correlation between GLX/GABA and the visual impairment is reported, but this is specific to the patients group (N=10) and would not hold across groups (the correlation is positive, predicting the lowest GLX/GABA ratio values for the sighted controls - opposite of what is found). There is also a strong correlation between GLX concentrations and the EEG power at the lowest temporal frequencies. Although this relation is intriguing, it only holds for a very specific combination of parameters (of the many tested): only with eyes open, only in the patients group.

Conclusions:

The main claim of the study is that sight recovery impacts the excitation/inhibition balance in the visual cortex, estimated with MRS or through indirect EEG indices. However, due to the weaknesses outlined above, the study cannot distinguish the effects of sight recovery from those of visual deprivation. Moreover, many aspects of the results are interesting but their validation and interpretation require additional experimental work.

Comments on revisions:

The authors' revisions did not substantially alter the manuscript. As such, my assessment above remains unaltered.

Reviewer #3 (Public review):

Summary:

This manuscript examines the impact of congenital visual deprivation on the excitatory/inhibitory (E/I) ratio in the visual cortex using Magnetic Resonance Spectroscopy (MRS) and electroencephalography (EEG) in individuals whose sight was restored. Ten individuals with reversed congenital cataracts were compared to age-matched, normally sighted controls, assessing the cortical E/I balance and its interrelationship and to visual acuity. The study reveals that the Glx/GABA ratio in the visual cortex and the intercept and aperiodic signal are significantly altered in those with a history of early visual deprivation, suggesting persistent neurophysiological changes despite visual restoration. First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods. Second, although the authors addressed some of my concerns on the previous version of this manuscript, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over) interpretation of the results.

Persistent specific concerns include:<br /> (1 3.1) Response to Variability in Visual Deprivation<br /> Rather than listing the advantages and disadvantages of visual deprivation, I recommend providing at least a descriptive analysis of how the duration of visual deprivation influenced the measures of interest. This would enhance the depth and relevance of the discussion.

(2 3.2) Small Sample Size<br /> The issue of small sample size remains problematic. The justification that previous studies employed similar sample sizes does not adequately address the limitation in the current study. I strongly suggest that the correlation analyses should not feature prominently in the main manuscript or the abstract, especially if the discussion does not substantially rely on these correlations. Please also revisit the recommendations made in the section on statistical concerns.

(3 3.3) Statistical Concerns<br /> While I appreciate the effort of conducting an independent statistical check, it merely validates whether the reported statistical parameters, degrees of freedom (df), and p-values are consistent. However, this does not address the appropriateness of the chosen statistical methods.

Several points require clarification or improvement:

(4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.<br /> This has been addressed in the final revision

(5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.<br /> This has been addressed in the final revision

(6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.

(7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.<br /> This has been addressed in the final revision

(8) Figure 2C<br /> Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.

(9 3.4) Interpretation of Aperiodic Signal<br /> Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.

(10) Additionally, the authors state:<br /> "We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."

(11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.

(12 3.5) Problems with EEG Preprocessing and Analysis<br /> Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal asE/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz oreven 1-45 Hz (not 20-40 Hz).

(13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis.

(14) The authors mention: "The EEG data sets reported here were part of data published earlier (Ossandón et al.,2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."<br /> The authors addressed this comment and adjusted the statement. However, I do not understand, why the full sample published earlier (Ossandón et al., 2023) was not used in the current study?

Comments on revisions:

The current version of the manuscript is almost unchanged compared to the last version. Unfortunately, I observed that the authors have not adequately addressed most of my previous suggestions; rather, they provided justifications for not incorporating them.

Given this, I do not see the need to modify my initial assessment.

Author response:

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

eLife Assessment

This neuroimaging and electrophysiology study in a small cohort of congenital cataract patients with sight recovery aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in visual cortex. While contrasting sight-recovery with visually intact controls suggested the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, it provided only incomplete evidence supporting claims about the effects of early deprivation itself. The reported data were considered valuable, given the rare study population. However, the small sample sizes, lack of a specific control cohort and multiple methodological limitations will likely restrict usefulness to scientists working in this particular subfield.

We thank the reviewing editors for their consideration and updated assessment of our manuscript after its first revision.

In order to assess the effects of early deprivation, we included an age-matched, normally sighted control group recruited from the same community, measured in the same scanner and laboratory. This study design is analogous to numerous studies in permanently congenitally blind humans, which typically recruited sighted controls, but hardly ever individuals with a different, e.g. late blindness history. In order to improve the specificity of our conclusions, we used a frontal cortex voxel in addition to a visual cortex voxel (MRS). Analogously, we separately analyzed occipital and frontal electrodes (EEG).

Moreover, we relate our findings in congenital cataract reversal individuals to findings in the literature on permanent congenital blindness. Note, there are, to the best of our knowledge, neither MRS nor resting-state EEG studies in individuals with permanent late blindness.

Our participants necessarily have nystagmus and low visual acuity due to their congenital deprivation phase, and the existence of nystagmus is a recruitment criterion to diagnose congenital cataracts.

It might be interesting for future studies to investigate individuals with transient late blindness. However, such a study would be ill-motivated had we not found differences between the most “extreme” of congenital visual deprivation conditions and normally sighted individuals (analogous to why earlier research on permanent blindness investigated permanent congenitally blind humans first, rather than permanently late blind humans, or both in the same study). Any result of these future work would need the reference to our study, and neither results in these additional groups would invalidate our findings.

Since all our congenital cataract reversal individuals by definition had visual impairments, we included an eyes closed condition, both in the MRS and EEG assessment. Any group effect during the eyes closed condition cannot be due to visual acuity deficits changing the bottom-up driven visual activation.

As we detail in response to review 3, our EEG analyses followed the standards in the field.

Public Reviews:

Reviewer #1 (Public review):

Summary

In this human neuroimaging and electrophysiology study, the authors aimed to characterise effects of a period of visual deprivation in the sensitive period on excitatory and inhibitory balance in the visual cortex. They attempted to do so by comparing neurochemistry conditions ('eyes open', 'eyes closed') and resting state, and visually evoked EEG activity between ten congenital cataract patients with recovered sight (CC), and ten age-matched control participants (SC) with normal sight.

First, they used magnetic resonance spectroscopy to measure in vivo neurochemistry from two locations, the primary location of interest in the visual cortex, and a control location in the frontal cortex. Such voxels are used to provide a control for the spatial specificity of any effects, because the single-voxel MRS method provides a single sampling location. Using MR-visible proxies of excitatory and inhibitory neurotransmission, Glx and GABA+ respectively, the authors report no group effects in GABA+ or Glx, no difference in the functional conditions 'eyes closed' and 'eyes open'. They found an effect of group in the ratio of Glx/GABA+ and no similar effect in the control voxel location. They then perform multiple exploratory correlations between MRS measures and visual acuity, and report a weak positive correlation between the 'eyes open' condition and visual acuity in CC participants.

The same participants then took part in an EEG experiment. The authors selected two electrodes placed in the visual cortex for analysis and report a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. Control electrodes in the frontal region did not present with the same pattern. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

The authors report the difference in E/I ratio, and interpret the lower E/I ratio as representing an adaptation to visual deprivation, which would have initially caused a higher E/I ratio. Although intriguing, the strength of evidence in support of this view is not strong. Amongst the limitations are the low sample size, a critical control cohort that could provide evidence for higher E/I ratio in CC patients without recovered sight for example, and lower data quality in the control voxel. Nevertheless, the study provides a rare and valuable insight into experience-dependent plasticity in the human brain.

Strengths of study

How sensitive period experience shapes the developing brain is an enduring and important question in neuroscience. This question has been particularly difficult to investigate in humans. The authors recruited a small number of sight-recovered participants with bilateral congenital cataracts to investigate the effect of sensitive period deprivation on the balance of excitation and inhibition in the visual brain using measures of brain chemistry and brain electrophysiology. The research is novel, and the paper was interesting and well written.

Limitations

Low sample size. Ten for CC and ten for SC, and further two SC participants were rejected due to lack of frontal control voxel data. The sample size limits the statistical power of the dataset and increases the likelihood of effect inflation.

In the updated manuscript, the authors have provided justification for their sample size by pointing to prior studies and the inherent difficulties in recruiting individuals with bilateral congenital cataracts. Importantly, this highlights the value the study brings to the field while also acknowledging the need to replicate the effects in a larger cohort.

Lack of specific control cohort. The control cohort has normal vision. The control cohort is not specific enough to distinguish between people with sight loss due to different causes and patients with congenital cataracts with co-morbidities. Further data from a more specific populations, such as patients whose cataracts have not been removed, with developmental cataracts, or congenitally blind participants, would greatly improve the interpretability of the main finding. The lack of a more specific control cohort is a major caveat that limits a conclusive interpretation of the results.

In the updated version, the authors have indicated that future studies can pursue comparisons between congenital cataract participants and cohorts with later sight loss.

MRS data quality differences. Data quality in the control voxel appears worse than in the visual cortex voxel. The frontal cortex MRS spectrum shows far broader linewidth than the visual cortex (Supplementary Figures). Compared to the visual voxel, the frontal cortex voxel has less defined Glx and GABA+ peaks; lower GABA+ and Glx concentrations, lower NAA SNR values; lower NAA concentrations. If the data quality is a lot worse in the FC, then small effects may not be detectable.

In the updated version, the authors have added more information that informs the reader of the MRS quality differences between voxel locations. This increases the transparency of their reporting and enhances the assessment of the results.

Because of the direction of the difference in E/I, the authors interpret their findings as representing signatures of sight improvement after surgery without further evidence, either within the study or from the literature. However, the literature suggests that plasticity and visual deprivation drives the E/I index up rather than down. Decreasing GABA+ is thought to facilitate experience dependent remodelling. What evidence is there that cortical inhibition increases in response to a visual cortex that is over-sensitised to due congenital cataracts? Without further experimental or literature support this interpretation remains very speculative.

The updated manuscript contains key reference from non-human work to justify their interpretation.

Heterogeneity in patient group. Congenital cataract (CC) patients experienced a variety of duration of visual impairment and were of different ages. They presented with co-morbidities (absorbed lens, strabismus, nystagmus). Strabismus has been associated with abnormalities in GABAergic inhibition in the visual cortex. The possible interactions with residual vision and confounds of co-morbidities are not experimentally controlled for in the correlations, and not discussed.

The updated document has addressed this caveat.

Multiple exploratory correlations were performed to relate MRS measures to visual acuity (shown in Supplementary Materials), and only specific ones shown in the main document. The authors describe the analysis as exploratory in the 'Methods' section. Furthermore, the correlation between visual acuity and E/I metric is weak, not corrected for multiple comparisons. The results should be presented as preliminary, as no strong conclusions can be made from them. They can provide a hypothesis to test in a future study.

This has now been done throughout the document and increases the transparency of the reporting.

P.16 Given the correlation of the aperiodic intercept with age ("Age negatively correlated with the aperiodic intercept across CC and SC individuals, that is, a flattening of the intercept was observed with age"), age needs to be controlled for in the correlation between neurochemistry and the aperiodic intercept. Glx has also been shown to negatively correlates with age.

This caveat has been addressed in the revised manuscript.

Multiple exploratory correlations were performed to relate MRS to EEG measures (shown in Supplementary Materials), and only specific ones shown in the main document. Given the multiple measures from the MRS, the correlations with the EEG measures were exploratory, as stated in the text, p.16, and in Fig.4. yet the introduction said that there was a prior hypothesis "We further hypothesized that neurotransmitter changes would relate to changes in the slope and intercept of the EEG aperiodic activity in the same subjects." It would be great if the text could be revised for consistency and the analysis described as exploratory.

This has been done throughout the document and increases the transparency of the reporting.

The analysis for the EEG needs to take more advantage of the available data. As far as I understand, only two electrodes were used, yet far more were available as seen in their previous study (Ossandon et al., 2023). The spatial specificity is not established. The authors could use the frontal cortex electrode (FP1, FP2) signals as a control for spatial specificity in the group effects, or even better, all available electrodes and correct for multiple comparisons. Furthermore, they could use the aperiodic intercept vs Glx in SC to evaluate the specificity of the correlation to CC.

This caveat has been addressed. The authors have added frontal electrodes to their analysis, providing an essential regional control for the visual cortex location.

Comments on the latest version:

The authors have made reasonable adjustments to their manuscript that addressed most of my comments by adding further justification for their methodology, essential literature support, pointing out exploratory analyses, limitations and adding key control analyses. Their revised manuscript has overall improved, providing valuable information, though the evidence that supports their claims is still incomplete.

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Reviewer #2 (Public review):

Summary:

The study examined 10 congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts, measuring neural activity and neuro chemical profiles from the visual cortex. The declared aim is to test whether restoring visual function after years of complete blindness impacts excitation/inhibition balance in the visual cortex.

Strengths:

The findings are undoubtedly useful for the community, as they contribute towards characterising the many ways in which this special population differs from normally sighted individuals. The combination of MRS and EEG measures is a promising strategy to estimate a fundamental physiological parameter - the balance between excitation and inhibition in the visual cortex, which animal studies show to be heavily dependent upon early visual experience. Thus, the reported results pave the way for further studies, which may use a similar approach to evaluate more patients and control groups.

Weaknesses:

The main methodological limitation is the lack of an appropriate comparison group or condition to delineate the effect of sight recovery (as opposed to the effect of congenital blindness). Few previous studies suggested that Excitation/Inhibition ratio in the visual cortex is increased in congenitally blind patients; the present study reports that E/I ratio decreases instead. The authors claim that this implies a change of E/I ratio following sight recovery. However, supporting this claim would require showing a shift of E/I after vs. before the sight-recovery surgery, or at least it would require comparing patients who did and did not undergo the sight-recovery surgery (as common in the field).

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Since we have not been able to acquire longitudinal data with the experimental design of the present study in congenital cataract reversal individuals, we compared the MRS and EEG results of congenital cataract reversal individuals  to published work in congenitally permanent blind individuals. We consider this as a resource saving approach. We think that the results of our cross-sectional study now justify the costs and enormous efforts (and time for the patients who often have to travel long distances) associated with longitudinal studies in this rare population.

There are also more technical limitations related to the correlation analyses, which are partly acknowledged in the manuscript. A bland correlation between GLX/GABA and the visual impairment is reported, but this is specific to the patients group (N=10) and would not hold across groups (the correlation is positive, predicting the lowest GLX/GABA ratio values for the sighted controls - opposite of what is found). There is also a strong correlation between GLX concentrations and the EEG power at the lowest temporal frequencies. Although this relation is intriguing, it only holds for a very specific combination of parameters (of the many tested): only with eyes open, only in the patients group.

Given the exploratory nature of the correlations, we do not base the majority of our conclusions on this analysis. There are no doubts that the reported correlations need replication; however, replication is only possible after a first report. Thus, we hope to motivate corresponding analyses in further studies.

It has to be noted that in the present study significance testing for correlations were corrected for multiple comparisons, and that some findings replicate earlier reports (e.g. effects on EEG aperiodic slope, alpha power, and correlations with chronological age).

Conclusions:

The main claim of the study is that sight recovery impacts the excitation/inhibition balance in the visual cortex, estimated with MRS or through indirect EEG indices. However, due to the weaknesses outlined above, the study cannot distinguish the effects of sight recovery from those of visual deprivation. Moreover, many aspects of the results are interesting but their validation and interpretation require additional experimental work.

We interpret the group differences between individuals tested years after congenital visual deprivation and normally sighted individuals as supportive of the E/I ratio being impacted by congenital visual deprivation. In the absence of a sensitive period for the development of an E/I ratio, individuals with a transient phase of congenital blindness might have developed a visual system indistinguishable  from normally sighted individuals. As we demonstrate, this is not so. Comparing the results of congenitally blind humans with those of congenitally permanently blind humans (from previous studies) allowed us to identify changes of E/I ratio, which add to those found for congenital blindness.  

We thank the reviewer for the helpful comments and suggestions related to the first submission and first revision of our manuscript. We are keen to translate some of them into future studies.

Reviewer #3 (Public review):

This manuscript examines the impact of congenital visual deprivation on the excitatory/inhibitory (E/I) ratio in the visual cortex using Magnetic Resonance Spectroscopy (MRS) and electroencephalography (EEG) in individuals whose sight was restored. Ten individuals with reversed congenital cataracts were compared to age-matched, normally sighted controls, assessing the cortical E/I balance and its interrelationship and to visual acuity. The study reveals that the Glx/GABA ratio in the visual cortex and the intercept and aperiodic signal are significantly altered in those with a history of early visual deprivation, suggesting persistent neurophysiological changes despite visual restoration.

First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods.

Although the authors addressed some of the concerns of the previous version, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over)interpretation of the results. Specific concerns include:

(1 3.1) Response to Variability in Visual Deprivation<br /> Rather than listing the advantages and disadvantages of visual deprivation, I recommend providing at least a descriptive analysis of how the duration of visual deprivation influenced the measures of interest. This would enhance the depth and relevance of the discussion.

Although Review 2 and Review 3 (see below) pointed out problems in interpreting multiple correlational analyses in small samples, we addressed this request by reporting such correlations between visual deprivation history and measured EEG/MRS outcomes.

Calculating the correlation between duration of visual deprivation and behavioral or brain measures is, in fact, a common suggestion. The existence of sensitive periods, which are typically assumed to not follow a linear gradual decline of neuroplasticity, does not necessary allow predicting a correlation with duration of blindness. Daphne Maurer has additionally worked on the concept of “sleeper effects” (Maurer et al., 2007), that is, effects on the brain and behavior by early deprivation which are observed only later in life when the function/neural circuits matures.

In accordance with this reasoning, we did not observe a significant correlation between duration of visual deprivation and any of our dependent variables.

(2 3.2) Small Sample Size<br /> The issue of small sample size remains problematic. The justification that previous studies employed similar sample sizes does not adequately address the limitation in the current study. I strongly suggest that the correlation analyses should not feature prominently in the main manuscript or the abstract, especially if the discussion does not substantially rely on these correlations. Please also revisit the recommendations made in the section on statistical concerns.

In the revised manuscript, we explicitly mention that our sample size is not atypical for the special group investigated, but that a replication of our results in larger samples would foster their impact. We only explicitly mention correlations that survived stringent testing for multiple comparisons in the main manuscript.

Given the exploratory nature of the correlations, we have not based the majority of our claims on this analysis.

(3 3.3) Statistical Concerns<br /> While I appreciate the effort of conducting an independent statistical check, it merely validates whether the reported statistical parameters, degrees of freedom (df), and p-values are consistent. However, this does not address the appropriateness of the chosen statistical methods.

We did not intend for the statcheck report to justify the methods used for statistics, which we have done in a separate section with normality and homogeneity testing (Supplementary Material S9), and references to it in the descriptions of the statistical analyses (Methods, Page 13, Lines 326-329 and Page 15, Lines 400-402).

Several points require clarification or improvement:<br /> (4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.

The depicted correlations are Pearson correlations. We will add this information to the Methods.

(5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.

We have added the confidence intervals for all measured correlations to the second revision of our manuscript.

(6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.

Our study focuses on a rare population, with a sample size limited by the availability of participants. Our findings provide exploratory insights rather than make strong inferential claims. To this end, we have ensured that our analysis adheres to key statistical assumptions (Shapiro-Wilk as well as Levene’s tests, Supplementary Material S9), and reported our findings with effect sizes, appropriate caution and context.

(7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.

In the revised manuscript, we have changed Figure 4 to say ‘adjusted p,’  which we indeed reported.

(8) Figure 2C

Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.

Figure 2C depicts the correlation between Glx/GABA+ ratio and visual acuity in the congenital cataract reversal group, not the control group. This is mentioned in the Figure 2 legend, as well as in the main text where the figure is referred to (Page 18, Line 475).

The correlation analyses between visual acuity and MRS/EEG measures were only performed in the congenital cataract reversal group since the sighed control group comprised of individuals with vision in the normal range; thus this analyses would not make sense. Table 1 with the individual visual acuities for all participants, including the normally sighted controls, shows the low variance in the latter group.  

For variables in which no apiori group differences in variance were predicted, we performed the correlation analyses across groups (see Supplementary Material S12, S15).

We have now highlighted these motivations more clearly in the Methods of the revised manuscript (Page 16, Lines 405-410).

(9 3.4) Interpretation of Aperiodic Signal

Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.

How to interpret aperiodic EEG activity has been subject of extensive investigation. We cite studies which provide evidence from multiple species (monkeys, humans) and measurements (EEG, MEG, ECoG), including studies which pharmacologically manipulated E/I balance.

Whether our findings are robust, in fact, requires a replication study. Importantly, we analyzed the intercept of the aperiodic activity fit as well, and discuss results related to the intercept.

Quote:

“(3.4) Interpretation of aperiodic signal:

- Several recent papers demonstrated that the aperiodic signal measured in EEG or ECoG is related to various important aspects such as age, skull thickness, electrode impedance, as well as cognition. Thus, currently, very little is known about the underlying effects which influence the aperiodic intercept and slope. The entire interpretation of the aperiodic slope as a proxy for E/I is based on a computational model and simulation (as described in the Gao et al. paper).

Apart from the modeling work from Gao et al., multiple papers which have also been cited which used ECoG, EEG and MEG and showed concomitant changes in aperiodic activity with pharmacological manipulation of the E/I ratio (Colombo et al., 2019; Molina et al., 2020; Muthukumaraswamy & Liley, 2018). Further, several prior studies have interpreted changes in the aperiodic slope as reflective of changes in the E/I ratio, including studies of developmental groups (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Schaworonkow & Voytek, 2021) as well as patient groups (Molina et al., 2020; Ostlund et al., 2021).

- The authors further wrote: We used the slope of the aperiodic (1/f) component of the EEG spectrum as an estimate of E/I ratio (Gao et al., 2017; Medel et al., 2020; Muthukumaraswamy & Liley, 2018). This is a highly speculative interpretation with very little empirical evidence. These papers were conducted with ECoG data (mostly in animals) and mostly under anesthesia. Thus, these studies only allow an indirect interpretation by what the 1/f slope in EEG measurements is actually influenced.

Note that Muthukumaraswamy et al. (2018) used different types of pharmacological manipulations and analyzed periodic and aperiodic MEG activity in humans, in addition to monkey ECoG (Muthukumaraswamy & Liley, 2018). Further, Medel et al. (now published as Medel et al., 2023) compared EEG activity in addition to ECoG data after propofol administration. The interpretation of our results are in line with a number of recent studies in developing (Hill et al., 2022; Schaworonkow & Voytek, 2021) and special populations using EEG. As mentioned above, several prior studies have used the slope of the 1/f component/aperiodic activity as an indirect measure of the E/I ratio (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Molina et al., 2020; Ostlund et al., 2021; Schaworonkow & Voytek, 2021), including studies using scalp-recorded EEG from humans.

In the introduction of the revised manuscript, we have made more explicit that this metric is indirect (Page 3, Line 91), (additionally see Discussion, Page 24, Lines 644-645, Page 25, Lines 650-657).

While a full understanding of aperiodic activity needs to be provided, some convergent ideas have emerged. We think that our results contribute to this enterprise, since our study is, to the best of our knowledge, the first which assessed MRS measured neurotransmitter levels and EEG aperiodic activity. “

(10) Additionally, the authors state:

"We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."

(11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.

We are not aware of any study that would justify such an analysis.

Our analyses were based on previous findings in the literature.

Since to the best of our knowledge, no evidence exists that congenital cataracts go together with changes in skull thickness, and that skull thickness might selectively modulate visual cortex Glx/GABA+ but not NAA measures, we decided against following this suggestion.

Notably, the neurotransmitter concentration reported here is after tissue segmentation of the voxel region. The tissue fraction was shown to not differ between groups in the MRS voxels (Supplementary Material S4). The EEG electrode impedance was lowered to <10 kOhm in every participant (Methods, Page 13, Line 344), and preparation was identical across groups.

(12 3.5) Problems with EEG Preprocessing and Analysis

Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal as E/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz or even 1-45 Hz (not 20-40 Hz).

As previously mentied in the Methods (Page 15 Line 376) and the previous response, the pop_resample function used by EEGLAB applies an anti-aliasing filter, at half the resampling frequency (as per the Nyquist theorem

https://eeglab.org/tutorials/05_Preprocess/resampling.html). The upper cut off of the low pass filter set by EEGlab prior to down sampling (30 Hz) is still far above the frequency of interest in the current study  (1-20 Hz), thus allowing us to derive valid results.

Quote:

“- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which ranged in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; Vanrullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .”

Moreover, the resting-state data were not resampled to 60 Hz. We have made this clearer in the Methods of the second revision (Page 15, Line 367).

Our consistent results of group differences across all three EEG conditions, thus, exclude any possibility that they were driven by aliasing artifacts.

The expected effects of this anti-aliasing filter can be seen in the attached Author response image 1, showing an example participant’s spectrum in the 1-30 Hz range (as opposed to the 1-20 Hz plotted in the manuscript), clearly showing a 30-40 dB drop at 30 Hz. Any aliasing due to, for example, remaining line noise, would additionally be visible in this figure (as well as Figure 3) as a peak.

Author response image 1.

Power spectral density of one congenital cataract-reversal (CC) participant in the visual stimulation condition across all channels. The reduced power at 30 Hz shows the effects of the anti-aliasing filter applied by EEGLAB’s pop_resample function.

As we stated in the manuscript, and in previous reviews, so far there has been no consensus on the exact range of measuring aperiodic activity. We made a principled decision based on the literature (showing a knee in aperiodic fits of this dataset at 20 Hz) (Medel et al., 2023; Ossandón et al., 2023), data quality (possible contamination by line noise at higher frequencies) and the purpose of the visual stimulation experiment (to look at the lower frequency range by stimulating up to 60 Hz, thereby limiting us to quantifying below 30 Hz), that 1-20 Hz would be the fit range in this dataset.

Quote:

“(3) What's the underlying idea of analyzing two separate aperiodic slopes (20-40Hz and 1-19Hz). This is very unusual to compute the slope between 20-40 Hz, where the SNR is rather low.

"Ossandón et al. (2023), however, observed that in addition to the flatter slope of the aperiodic power spectrum in the high frequency range (20-40 Hz), the slope of the low frequency range (1-19 Hz) was steeper in both, congenital cataract-reversal individuals, as well as in permanently congenitally blind humans."

The present manuscript computed the slope between 1-20 Hz. Ossandón et al. as well as Medel et al. (2023) found a “knee” of the 1/f distribution at 20 Hz and describe further the motivations for computing both slope ranges. For example, Ossandón et al. used a data driven approach and compared single vs. dual fits and found that the latter fitted the data better. Additionally, they found the best fit if a knee at 20 Hz was used. We would like to point out that no standard range exists for the fitting of the 1/f component across the literature and, in fact, very different ranges have been used (Gao et al., 2017; Medel et al., 2023; Muthukumaraswamy & Liley, 2018). “

(13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis. If I were reviewing for another journal, I would recommend rejection based on these flaws.

The baseline removal step from each epoch serves to remove the DC component of the recording and detrend the data. This is a standard preprocessing step (included as an option in preprocessing pipelines recommended by the EEGLAB toolbox, FieldTrip toolbox and MNE toolbox), additionally necessary to improve the efficacy of ICA decomposition (Groppe et al., 2009).

In the previous review round, a clarification of the baseline timing was requested, which we added. Beyond this request, there was no mention of the appropriateness of the baseline removal and/or a request to provide reasons for why it might not undermine the validity of the analysis.

Quote:

“- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has been explicitly stated in the revised manuscript (Page 13, Line 354).”

Prior work in the time (not frequency) domain on event-related potential (ERP) analysis has suggested that the baselining step might cause spurious effects (Delorme, 2023) (although see (Tanner et al., 2016)). We did not perform ERP analysis at any stage. One recent study suggests spurious group differences in the 1/f signal might be driven by an inappropriate dB division baselining method (Gyurkovics et al., 2021), which we did not perform.

Any effect of our baselining procedure on the FFT spectrum would be below the 1 Hz range, which we did not analyze.  

Each of the preprocessing steps in the manuscript match pipelines described and published in extensive prior work. We document how multiple aspects of our EEG results replicate prior findings (Supplementary Material S15, S18, S19), reports of other experimenters, groups and locations, validating that our results are robust.

We therefore reject the claim of methodological flaws in our EEG analyses in the strongest possible terms.

Quote:

“(3.5) Problems with EEG preprocessing and analysis:

- It seems that the authors did not identify bad channels nor address the line noise issue (even a problem if a low pass filter of below-the-line noise was applied).

As pointed out in the methods and Figure 1, we only analyzed data from two occipital channels, O1 and O2 neither of which were rejected for any participant. Channel rejection was performed for the larger dataset, published elsewhere (Ossandón et al., 2023; Pant et al., 2023). As control sites we added the frontal channels FP1 and Fp2 (see Supplementary Material S14)

Neither Ossandón et al. (2023) nor Pant et al. (2023) considered frequency ranges above 40 Hz to avoid any possible contamination with line noise. Here, we focused on activity between 0 and 20 Hz, definitely excluding line noise contaminations (Methods, Page 14, Lines 365-367). The low pass filter (FIR, 1-45 Hz) guaranteed that any spill-over effects of line noise would be restricted to frequencies just below the upper cutoff frequency.

Additionally, a prior version of the analysis used spectrum interpolation to remove line noise; the group differences remained stable (Ossandón et al., 2023). We have reported this analysis in the revised manuscript (Page 14, Lines 364-357).

Further, both groups were measured in the same lab, making line noise (~ 50 Hz) as an account for the observed group effects in the 1-20 Hz frequency range highly unlikely. Finally, any of the exploratory MRS-EEG correlations would be hard to explain if the EEG parameters would be contaminated with line noise.

- What was the percentage of segments that needed to be rejected due to the 120μV criteria? This should be reported specifically for EO & EC and controls and patients.

The mean percentage of 1 second segments rejected for each resting state condition and the percentage of 6.25 long segments rejected in each group for the visual stimulation condition have been added to the revised manuscript (Supplementary Material S10), and referred to in the Methods on Page 14, Lines 372-373).

- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which changed in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; VanRullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .

- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has now been explicitly stated in the revised manuscript (Page 14, Lines 379-380).

- "We excluded the alpha range (8-14 Hz) for this fit to avoid biasing the results due to documented differences in alpha activity between CC and SC individuals (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023)." This does not really make sense, as the FOOOF algorithm first fits the 1/f slope, for which the alpha activity is not relevant.

We did not use the FOOOF algorithm/toolbox in this manuscript. As stated in the Methods, we used a 1/f fit to the 1-20 Hz spectrum in the log-log space, and subtracted this fit from the original spectrum to obtain the corrected spectrum. Given the pronounced difference in alpha power between groups (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023), we were concerned it might drive differences in the exponent values. Our analysis pipeline had been adapted from previous publications of our group and other labs (Ossandón et al., 2023; Voytek et al., 2015; Waschke et al., 2017).

We have conducted the analysis with and without the exclusion of the alpha range, as well as using the FOOOF toolbox both in the 1-20 Hz and 20-40 Hz ranges (Ossandón et al., 2023). The findings of a steeper slope in the 1-20 Hz range as well as lower alpha power in CC vs SC individuals remained stable. In Ossandón et al., the comparison between the piecewise fits and FOOOF fits led the authors to use the former, as it outperformed the FOOOF algorithm for their data.

- The model fits of the 1/f fitting for EO, EC, and both participant groups should be reported.

In Figure 3 of the manuscript, we depicted the mean spectra and 1/f fits for each group.

In the revised manuscript, we added the fit quality metrics (average R² values > 0.91 for each group and condition) (Methods Page 15, Lines 395-396; Supplementary Material S11) and additionally show individual subjects’ fits (Supplementary Material S11). “

(14) The authors mention:

"The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."

The authors addressed this comment and adjusted the statement. However, I do not understand, why not the full sample published earlier (Ossandón et al., 2023) was used in the current study?

The recording of EEG resting state data stated in 2013, while MRS testing could only be set up by the second half of 2019. Moreover, not all subjects who qualify for EEG recording qualify for being scanned (e.g. due to MRI safety, claustrophobia)

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eLife Assessment

van Vliet and colleagues show a useful correlation between internal states of a convolutional neural network (CNN) trained on visual word stimuli with three specific components of evoked MEG potentials during reading in humans. The findings are solid, though quantitative evidence that model can produce any of the phenomena that the human visual system is known to have (e.g., feedback connections, sensitivity to word frequency), or that it has comparable performance to human behaviour (i.e., similar task accuracy with a comparable pattern of mistakes) would make the conclusions much stronger.

Reviewer #2 (Public review):

van Vliet and colleagues present results of a study correlating internal states of a convolutional neural network trained on visual word stimuli with evoked MEG potentials during reading.

In this study, a standard deep learning image recognition model (VGG-11) trained on a large natural image set (ImageNet) that begins illiterate but is then further trained on visual word stimuli, is used on a set of predefined stimulus images to extract strings of characters from "noisy" words, pseudowords and real words. This methodology is used in hopes of creating a model which learns to apply the same nonlinear transforms that could be happening in different regions of the brain - which would be validated by studying the correlations between the weights of this model and neural responses. Specifically, the aim is that the model learns some vector embedding space, as quantified by the spread of activations across a layer's weights (L2 Norm prior to ReLu Activation Function), for the different kinds of stimuli, that creates a parameterized decision boundary that is similar to amplitude changes at different times for a MEG signal. More importantly, the way that the stimuli are ordered or ranked in that space should be separable to the degree we see separation in neural activity. This study does show that the layer weights corresponding to five different broad classes of stimuli do statistically correlate with three specific components in the ERP. However, I believe there are fundamental theoretical issues that limit the implications of the results of this study.

As has been shown over many decades, there are many potential computational algorithms, with varied model architectures, that can perform the task of text recognition from an image. However, there is no evidence presented here that this particular algorithm has comparable performance to human behavior (i.e. similar accuracy with a comparable pattern of mistakes). This is a fundamental prerequisite before attempting to meaningfully correlate these layer activations to human neural activations. Therefore, it is unlikely that correlating these derived layer weights to neural activity provides meaningful novel insights into neural computation beyond what is seen using traditional experimental methods.

One example of a substantial discrepancy between this model and neural activations is that, while incorporating frequency weighting into the training data is shown to slightly increase neural correlation with the model, Figure 7 shows that no layer of the model appears directly sensitive to word frequency. This is in stark contrast to the strong neural sensitivity to word frequency seen in EEG (e.g. Dambacher et al 2006 Brain Research), fMRI (e.g. Kronbichler et al 2004 NeuroImage), MEG (e.g. Huizeling et al 2021 Neurobio. Lang.), and intracranial (e.g. Woolnough et al 2022 J. Neurosci.) recordings. Figure 7 also demonstrates that late stages of the model show a strong negative correlation with font size, whereas later stages of neural visual word processing are typically insensitive to differences in visual features, instead showing sensitivity to lexical factors.

Another example of the mismatch between this model and visual cortex is the lack of feedback connections in the model. Within visual cortex there are extensive feedback connections, with later processing stages providing recursive feedback to earlier stages. This is especially evident in reading, where feedback from lexical level processes feeds back to letter level processes (e.g. Heilbron et al 2020 Nature Comms.). This feedback is especially relevant for reading of words in noisy conditions, as tested in the current manuscript, as lexical knowledge enhances letter representation in visual cortex (the word superiority effect). This results in neural activity in multiple cortical areas varying over time, changing selectivity within a region at different measured time points (e.g. Woolnough et al 2021 Nature Human Behav.), which in the current study is simplified down to three discrete time windows, each attributed to different spatial locations.

The presented model needs substantial further development to be able to replicate, both behaviorally and neurally, many of the well-characterized phenomena seen in human behavior and neural recordings that are fundamental hallmarks of human visual word processing. Until that point it is unclear what novel contributions can be gleaned from correlating low dimensional model weights from these computational models with human neural data.

The revised version of this manuscript has not addressed these concerns.

Reviewer #3 (Public review):

Summary:

The authors investigate the extent to which the responses of different layers of a vision model (VGG-11) can be linked to the cascade of responses (namely, type-I, type-II and N400) in the human brain when reading words. To achieve maximal consistency between, they add noisy-activations to VGG and finetune it on a character recognition task. In this setup, they observe various similarities between the behavior of VGG and the brain when presented with various transformations of the words (added noise, font modification etc).

Strengths:<br /> - The paper is well written and well presented<br /> - The topic studied is interesting.<br /> - The fact that the response of the CNN on unseen experimental contrasts such as adding noise correlated with previous results on the brain is compelling.

Weaknesses:<br /> - The paper is rather qualitative in nature. In particular, the authors show that some resemblance exists between the behavior of some layers and some parts of the brain, but it is hard to quantitively understand how strong the resemblences are in each layer, and the exact impact of experimental settings such as the frequency balancing (which seems to only have a very moderate effect according to figure 5)<br /> - The experiments only consider a rather outdated vision model (VGG)

Comments on revisions:

After rebuttal, the authors significantly strengthened their results. I now find the paper much more convincing, and thank the author for their careful consideration of the reviewers' suggestions.

Author response:

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

We thank the reviewers for their efforts. They have pointed out several shortcomings and made very helpful suggestions. Based on their feedback, we have substantially revised the manuscript and feel the paper has been much improved because of it.

Notable changes are:

(1) As our model does not contain feed-back connections, the focus of the study is now more clearly communicated to be on feed-forward processes only, with appropriate justifications for this choice added to the Introduction and Discussion sections. Accordingly, the title has been changed to include the term “feed-forward”.

(2) The old Figure 5 has been removed in favor of reporting correlation scores to the right of the response profiles in other figures.

(3) We now discuss changes to the network architecture (new Figure 5) and fine-tuning of the hyperparameters (new Figure 6) in the main text instead of only the Supplementary Information.

(4) The discussion on qualitative versus quantitative analysis has been extended and given its own subsection entitled “On the importance of experimental contrasts and qualitative analysis of the model”.

Below, we address each point that the reviewers brought up in detail and outline what improvements we have made in the revision to address them.

Reviewer #1 (Public Review):

Summary:

This study trained a CNN for visual word classification and supported a model that can explain key functional effects of the evoked MEG response during visual word recognition, providing an explicit computational account from detection and segmentation of letter shapes to final word-form identification.

Strengths:

This paper not only bridges an important gap in modeling visual word recognition, by establishing a direct link between computational processes and key findings in experimental neuroimaging studies, but also provides some conditions to enhance biological realism.

Weaknesses:

The interpretation of CNN results, especially the number of layers in the final model and its relationship with the processing of visual words in the human brain, needs to be further strengthened.

We have experimented with the number of layers and the number of units in each layer. In the previous version of the manuscript, these results could be found in the supplementary information. For the revised version, we have brought some of these results into the main text and discuss them more thoroughly.

We have added a figure (Figure 5 in the revised manuscript) showing the impact of the number of convolution and fully-connected layers on the response profiles of the layers, as well as the correlation with the three MEG components.

We discuss the figure in the Results section as follows:

“Various variations in model architecture and training procedure were evaluated. We found that the number of layers had a large impact on the response patterns produced by the model (Figure 5). The original VGG-11 architecture defines 5 convolution layers and 3 fully connected layers (including the output layer). Removing a convolution layer (Figure 5, top row), or removing one of the fully connected layers (Figure 5, second row), resulted in a model that did exhibit an enlarged response to noisy stimuli in the early layers that mimics the Type-I response. However, such models failed to show a sufficiently diminished response to noisy stimuli in the later layers, hence failing to produce responses that mimic the Type-II or N400m, a failure which also showed as low correlation scores.

Adding an additional convolution layer (Figure 5, third row) resulted in a model where none of the layer response profiles mimics that of the Type-II response. The Type-II response is characterized by a reduced response to both noise and symbols, but an equally large response to consonant strings, real and pseudo words. However, in the model with an additional convolution layer, the consonant strings evoked a reduced response already in the first fully connected layer, which is a feature of the N400m rather than the Type-II. These kind of subtleties in the response pattern, which are important for the qualitative analysis, generally did not show quantitatively in the correlation scores, as the fully connected layers in this model correlate as well with the Type-II response as models that did show a response pattern that mimics the Type-II.

Adding an additional fully connected layer (Figure 5, fourth row) resulted in a model with similar response profiles and correlation with the MEG components as the original VGG-11 architecture (Figure 5, bottom row) The N400m-like response profile is now observed in the third fully connected layer rather than the output layer. However, the decrease in response to consonant strings versus real and pseudo words, which is typical of the N400m, is less distinct than in the original VGG-11 architecture.”

And in the Discussion section:

“In the model, convolution units are followed by pooling units, which serve the purpose of stratifying the response across changes in position, size and rotation within the receptive field of the pooling unit. Hence, the effect of small differences in letter shape, such as the usage of different fonts, was only present in the early convolution layers, in line with findings in the EEG literature (Chauncey et al., 2008; Grainger & Holcomb, 2009; Hauk & Pulvermüller, 2004). However, the ability of pooling units to stratify such differences depends on the size of their receptive field, which is determined by the number of convolution-and-pooling layers. As a consequence, the response profiles of the subsequent fully connected layers was also very sensitive to the number of convolution-and-pooling layers. The optimal number of such layers is likely dependent on the input size and pooling strategy. Given the VGG-11 design of doubling the receptive field after each layer, combined with an input size of 225×225 pixels, the optimal number of convolution-andpooling layers for our model was five, or the model would struggle to produce response profiles mimicking those of the Type-II component in the subsequent fully connected layers (Figure 5).”

Reviewer #1 (Recommendations For The Authors):

(1) The similarity between CNNs and human MEG responses, including type-I (100ms), type-II (150ms), and N400 (400ms) components, looks like separately, lacking the sequential properties among these three components. Is the recurrent neural network (RNN), which can be trained to process and convert a sequential data input into a specific sequential data output, a better choice?

When modeling sequential effects, meaning that the processing of the current word is influenced by the word that came before it, such as priming and top-down modulations, we agree that such a model would indeed require recurrency in its architecture. However, we feel that the focus of modeling efforts in reading has been overwhelmingly on the N400 and such priming effects, usually skipping over the pixel-to-letter process. So, for this paper, we were keen on exploring more basic effects such as noise and symbols versus letters on the type-I and type-II responses. And for these effects, a feed-forward model turns out to be sufficient, so we can keep the focus of this particular paper on bottom-up processes during single word reading, on which there is already a lot to say.

To clarify our focus on feed-forward process, we have modified the title of the paper to be:

“Convolutional networks can model the functional modulation of the MEG responses associated with feed-forward processes during visual word recognition” furthermore, we have revised the Introduction to highlight this choice, noting:

“Another limitation is that these models have primarily focused on feed-back lexicosemantic effects while oversimplifying the initial feed-forward processing of the visual input.

[…]

For this study, we chose to focus on modeling the early feed-forward processing occurring during visual word recognition, as the experimental setup in Vartiainen et al. (2011) was designed to demonstrate.

[…]

By doing so, we restrict ourselves to an investigation of how well the three evoked components can be explained by a feed-forward CNN in an experimental setting designed to demonstrate feed-forward effects. As such, the goal is not to present a complete model of all aspects of reading, which should include feed-back effects, but rather to demonstrate the effectiveness of using a model that has a realistic form of input when the aim is to align the model with the evoked responses observed during visual word recognition.”

And in the Discussion section:

“In this paper we have restricted our simulations to feed-forward processes. Now, the way is open to incorporate convolution-and-pooling principles in models of reading that simulate feed-back processes as well, which should allow the model to capture more nuance in the Type-II and N400m components, as well as extend the simulation to encompass a realistic semantic representation.”

(2) There is no clear relationship between the layers that signal needs to traverse in the model and the relative duration of the three components in the brain.

While some models offer a tentative mapping between layers and locations in the brain, none of the models we are aware of actually simulate time accurately and our model is no exception.

While we provide some evidence that the three MEG components are best modeled with different types of layers, and the type-I becomes somewhere before type-II and N400m is last in our model, the lack of timing information is a weakness of our model we have not been able to address. In our previous version, this already was the main topic of our “Limitations of the model” section, but since this weakness was pointed out by all reviewers, we have decided to widen our discussion of it:

“One important limitation of the current model is the lack of an explicit mapping from the units inside its layers to specific locations in the brain at specific times. The temporal ordering of the components is simulated correctly, with the response profile matching that of the type-I occurring the layers before those matching the type-II, followed by the N400m. Furthermore, every component is best modeled by a different type of layer, with the type-I best described by convolution-and-pooling, the type-II by fully-connected linear layers and the N400m by a one-hot encoded layer. However, there is no clear relationship between the number of layers the signal needs to traverse in the model to the processing time in the brain. Even if one considers that the operations performed by the initial two convolution layers happen in the retina rather than the brain, the signal needs to propagate through three more convolution layers to reach the point where it matches the type-II component at 140-200 ms, but only through one more additional layer to reach the point where it starts to match the N400m component at 300-500 ms. Still, cutting down on the number of times convolution is performed in the model seems to make it unable to achieve the desired suppression of noise (Figure 5). It also raises the question what the brain is doing during the time between the type-II and N400m component that seems to take so long. It is possible that the timings of the MEG components are not indicative solely of when the feed-forward signal first reaches a certain location, but are rather dictated by the resolution of feed-forward and feedback signals (Nour Eddine et al., 2024).”

See also our response to the next comment of the Reviewer, in which we dive more into the effect of the number of layers, which could be seen as a manipulation of time.

(3) I am impressed by the CNN that authors modified to match the human brain pattern for the visual word recognition process, by the increase and decrease of the number of layers. The result of this part was a little different from the author’s expectation; however, the author didn’t explain or address this issue.

We are glad to hear that the reviewer found these results interesting. Accordingly, we now discuss these results more thoroughly in the main text.

We have moved the figure from the supplementary information to the main text (Figure 5 in the revised manuscript). And describe the results in the Results section:

“Various variations in model architecture and training procedure were evaluated. We found that the number of layers had a large impact on the response patterns produced by the model (Figure 5). The original VGG-11 architecture defines 5 convolution layers and 3 fully connected layers (including the output layer). Removing a convolution layer (Figure 5, top row), or removing one of the fully connected layers (Figure 5, second row), resulted in a model that did exhibit an enlarged response to noisy stimuli in the early layers that mimics the Type-I response. However, such models failed to show a sufficiently diminished response to noisy stimuli in the later layers, hence failing to produce responses that mimic the Type-II or N400m, a failure which also showed as low correlation scores.

Adding an additional convolution layer (Figure 5, third row) resulted in a model where none of the layer response profiles mimics that of the Type-II response. The Type-II response is characterized by a reduced response to both noise and symbols, but an equally large response to consonant strings, real and pseudo words. However, in the model with an additional convolution layer, the consonant strings evoked a reduced response already in the first fully connected layer, which is a feature of the N400m rather than the Type-II. These kind of subtleties in the response pattern, which are important for the qualitative analysis, generally did not show quantitatively in the correlation scores, as the fully connected layers in this model correlate as well with the Type-II response as models that did show a response pattern that mimics the Type-II.

Adding an additional fully connected layer (Figure 5, fourth row) resulted in a model with similar response profiles and correlation with the MEG components as the original VGG-11 architecture (Figure 5, bottom row) The N400m-like response profile is now observed in the third fully connected layer rather than the output layer. However, the decrease in response to consonant strings versus real and pseudo words, which is typical of the N400m, is less distinct than in the original VGG-11 architecture.”

We also incorporated these results in the Discussion:

“However, the ability of pooling units to stratify such differences depends on the size of their receptive field, which is determined by the number of convolution-andpooling layers. This might also explain why, in later layers, we observed a decreased response to stimuli where text was rendered with a font size exceeding the receptive field of the pooling units (Figure 8). Hence, the response profiles of the subsequent fully connected layers was very sensitive to the number of convolution-and-pooling layers. This number is probably dependent on the input size and pooling strategy. Given the VGG11 design of doubling the receptive field after each layer, combined with an input size of 225x225 pixels, the optimal number of convolution-and-pooling layers for our model was five, or the model would struggle to produce response profiles mimicking those of the type-II component in the subsequent fully connected layers (Figure 5).

[…]

A minimum of two fully connected layers was needed to achieve this in our case, and adding more fully connected layers would make them behave more like the component (Figure 5).”

(4) Can the author explain why the number of layers in the final model is optimal by benchmarking the brain hierarchy?

We have incorporated the figure describing the correlation between each model and the MEG components (previously Figure 5) with the figures describing the response profiles (Figures 4 and 5 in the revised manuscript and Supplementary Figures 2-6). This way, we (and the reader) can now benchmark every model qualitatively and quantitatively.

As we stated in our response to the previous comment, we have added a more thorough discussion on the number of layers, which includes the justification for our choice for the final model. The benchmark we used was primarily whether the model shows the same response patterns as the Type I, Type II and N400 responses, which disqualifies all models with fewer than 5 convolution and 3 fully connected layers. Models with more layers also show the proper response patterns, however we see that there is actually very little difference in the correlation scores between different models. Hence, our justification for sticking with the original VGG11 architecture is that it produces the qualitative best response profiles, while having roughly the same (decently high) correlation with the MEG components. Furthermore, by sticking to the standard architecture, we make it slightly easier to replicate our results as one can use readily available pre-trained ImageNet weights.

As well as always discussing the correlation scores in tandem with the qualitative analysis, we have added the following statement to the Results:

“Based on our qualitative and quantitative analysis, the model variant that performed best overall was the model that had the original VGG11 architecture and was preinitialized from earlier training on ImageNet, as depicted in the bottom rows of Figure 4 and Figure 5.”

Reviewer #2 (Public Review):

As has been shown over many decades, many potential computational algorithms, with varied model architectures, can perform the task of text recognition from an image. However, there is no evidence presented here that this particular algorithm has comparable performance to human behavior (i.e. similar accuracy with a comparable pattern of mistakes). This is a fundamental prerequisite before attempting to meaningfully correlate these layer activations to human neural activations. Therefore, it is unlikely that correlating these derived layer weights to neural activity provides meaningful novel insights into neural computation beyond what is seen using traditional experimental methods.

We very much agree with the reviewer that a qualitative analysis of whether the model can explain experimental effects needs to happen before a quantitative analysis, such as evaluating model-brain correlation scores. In fact, this is one of the intended key points we wished to make.

As we discuss at length in the Introduction, “traditional” models of reading (those that do not rely on deep learning) are not able to recognize a word regardless of exact letter shape, size, and (up to a point) rotation. In this study, our focus is on these low-level visual tasks rather than high-level tasks concerning semantics. As the Reviewer correctly states, there are many potential computational algorithms able to perform these visual task at a human level and so we need to evaluate the model not only on its ability to mimic human accuracy but also on generating a comparable pattern of mistakes. In our case, we need a pattern of behavior that is indicative of the visual processes at the beginning of the reading pipeline. Hence, rather than relying on behavioral responses that are produced at the very end, we chose the evaluate the model based on three MEG components that provide “snapshots” of the reading process at various stages. These components are known to manifest a distinct pattern of “behavior” in the way they respond to different experimental conditions (Figure 2), akin to what to Reviewer refers to as a “pattern of mistakes”. The model was first evaluated on its ability to replicate the behavior of the MEG components in a qualitative manner (Figure 4). Only then do we move on to a quantitative correlation analysis. In this manner, we feel we are in agreement with the approach advocated by the Reviewer.

In the Introduction, we now clarify:

“Another limitation is that these models have primarily focused on feed-back lexicosemantic effects while oversimplifying the initial feed-forward processing of the visual input.

[…]

We sought to construct a model that is able to recognize words regardless of length, size, typeface and rotation, as well as humans can, so essentially perfectly, whilst producing activity that mimics the type-I, type-II, and N400m components which serve as snapshots of this process unfolding in the brain.

[…]

These variations were first evaluated on their ability to replicate the experimental effects in that study, namely that the type-I response is larger for noise embedded words than all other stimuli, the type-II response is larger for all letter strings than symbols, and that the N400m is larger for real and pseudowords than consonant strings. Once a variation was found that could reproduce these effects satisfactorily, it was further evaluated based on the correlation between the amount of activation of the units in the model and MEG response amplitude.”

To make this prerequisite more clear, we have removed what was previously Figure 5, which showed the correlation between the various models the MEG components out of the context of their response patterns. Instead, these correlation values are now always presented next to the response patterns (Figures 4 and 5, and Supplementary Figures 2-6 in the revised manuscript). This invites the reader to always consider these metrics in relation to one another.

One example of a substantial discrepancy between this model and neural activations is that, while incorporating frequency weighting into the training data is shown to slightly increase neural correlation with the model, Figure 7 shows that no layer of the model appears directly sensitive to word frequency. This is in stark contrast to the strong neural sensitivity to word frequency seen in EEG (e.g. Dambacher et al 2006 Brain Research), fMRI (e.g. Kronbichler et al 2004 NeuroImage), MEG (e.g. Huizeling et al 2021 Neurobio. Lang.), and intracranial (e.g. Woolnough et al 2022 J. Neurosci.) recordings. Figure 7 also demonstrates that the late stages of the model show a strong negative correlation with font size, whereas later stages of neural visual word processing are typically insensitive to differences in visual features, instead showing sensitivity to lexical factors.

We are glad the reviewer brought up the topic of frequency balancing, as it is a good example of the importance of the qualitative analysis. Frequency balancing during training only had a moderate impact on correlation scores and from that point of view does not seem impactful. However, when we look at the qualitative evaluation, we see that with a large vocabulary, a model without frequency balancing fails to properly distinguish between consonant strings and (pseudo)words (Figure 4, 5th row). Hence, from the point of view of being able to reproduce experimental effects, frequency balancing had a large impact. We now discuss this more explicitly in the revised Discussion section:

“Overall, we found that a qualitative evaluation of the response profiles was more helpful than correlation scores. Often, a deficit in the response profile of a layer that would cause a decrease in correlation on one condition would be masked by an increased correlation in another condition. A notable example is the necessity for frequency-balancing the training data when building models with a vocabulary of 10 000. Going by correlation score alone, there does not seem to be much difference between the model trained with and without frequency balancing (Figure 4A, fifth row versus bottom row). However, without frequency balancing, we found that the model did not show a response profile where consonant strings were distinguished from words and pseudowords (Figure 4A, fifth row), which is an important behavioral trait that sets the N400m component apart from the Type-II component (Figure 2D). This underlines the importance of the qualitative evaluation in this study, which was only possible because of a straightforward link between the activity simulated within a model to measurements obtained from the brain, combined with the presence of clear experimental conditions.”

It is true that the model, even with frequency balancing, only captures letter- and bigramfrequency effects and not the word-frequency effects that we know the N400m is sensitive to. Since our model is restricted to feed-forward processes, this finding adds to the evidence that frequency-modulated effects are driven by feed-back effects as modeled by Nour Eddine et al. (2024, doi:10.1016/j.cognition.2024.105755). See also our response to the next comment by the Reviewer where we discuss feed-back connections. We have added the following to the section about model limitations in the revised Discussion:

“The fact that the model failed to simulate the effects of word-frequency on the N400m (Figure 8), even after frequency-balancing of the training data, is additional evidence that this effect may be driven by feed-back activity, as for example modeled by Nour Eddine et al. (2024).”

Like the Reviewer, we initially thought that later stages of neural visual word processing would be insensitive to differences in font size. When diving into the literature to find support for this claim, we found only a few works directly studying the effect of font size on evoked responses, but, surprisingly, what we did find seemed to align with our model. We have added the following to our revised Discussion:

“The fully connected linear layers in the model show a negative correlation with font size. While the N400 has been shown to be unaffected by font size during repetition priming (Chauncey et al., 2008), it has been shown that in the absence of priming, larger font sizes decrease the evoked activity in the 300–500 ms window (Bayer et al., 2012; Schindler et al., 2018). Those studies refer to the activity within this time window, which seems to encompass the N400, as early posterior negativity (EPN). What possibly happens in the model is that an increase in font size causes an initial stronger activation in the first layers, due to more convolution units receiving input. This leads to a better signal-to-noise ratio (SNR) later on, as the noise added to the activation of the units remains constant whilst the amplitude of the input signal increases. A better SNR translates ultimately in less co-activation of units corresponding to orthographic neighbours in the final layers, hence to a decrease in overall layer activity.”

Another example of the mismatch between this model and the visual cortex is the lack of feedback connections in the model. Within the visual cortex, there are extensive feedback connections, with later processing stages providing recursive feedback to earlier stages. This is especially evident in reading, where feedback from lexical-level processes feeds back to letter-level processes (e.g. Heilbron et al 2020 Nature Comms.). This feedback is especially relevant for the reading of words in noisy conditions, as tested in the current manuscript, as lexical knowledge enhances letter representation in the visual cortex (the word superiority effect). This results in neural activity in multiple cortical areas varying over time, changing selectivity within a region at different measured time points (e.g. Woolnough et al 2021 Nature Human Behav.), which in the current study is simplified down to three discrete time windows, each attributed to different spatial locations.

We agree with the Reviewer that a full model of reading in the brain must include feed-back connections and share their sentiment that these feed-back processes play an important role and are a fascinating topic to study. The intent for the model presented in our study is very much to be a stepping stone towards extending the capabilities of models that do include such connections.

However, there is a problem of scale that cannot be ignored.

Current models of reading that do include feedback connections fall into the category we refer to in the paper as “traditional models” and all only a few layers deep and operate on very simplified inputs, such as pre-defined line segments, a few pixels, or even a list of prerecognized letters. The Heilbron et al. 2020 study that the Reviewer refers to is a good example of such a model. (This excellent and relevant work was somehow overlooked in our literature discussion in the Introduction. We thank the Reviewer for pointing it out to us.) Models incorporating realistic feed-back activity need these simplifications, because they have a tendency to no longer converge when there are too many layers and units. However, in order for models of reading to be able to simulate cognitive behavior such as resolving variations in font size or typeface, or distinguish text from non-text, they need to operate on something close to the pixel-level data, which means they need many layers and units.

Hence, as a stepping stone, it is reasonable to evaluate a model that has the necessary scale, but lacks the feed-back connections that would be problematic at this scale, to see what it can and cannot do in terms of explaining experimental effects in neuroimaging studies. This was the intended scope of our study. For the revision, we have attempted to make this more clear.

We have changed the title to be:

“Convolutional networks can model the functional modulation of the MEG responses associated with feed-forward processes during visual word recognition” and added the following to the Introduction:

“The simulated environments in these models are extremely simplified, partly due to computational limitations and partly due to the complex interaction of feed-forward and feed-back connectivity that causes problems with convergence when the model grows too large. Consequently, these models have primarily focused on feed-back lexico-semantic effects while oversimplifying the initial feed-forward processing of the visual input. 

[…]

This rather high level of visual representation sidesteps having to deal with issues such as visual noise, letters with different scales, rotations and fonts, segmentation of the individual letters, and so on. More importantly, it makes it impossible to create the visual noise and symbol string conditions used in the MEG study to modulate the type-I and type-II components. In order to model the process of visual word recognition to the extent where one may reproduce neuroimaging studies such as Vartiainen et al. (2011), we need to start with a model of vision that is able to directly operate on the pixels of a stimulus. We sought to construct a model that is able to recognize words regardless of length, size, typeface and rotation with very high accuracy, whilst producing activity that mimics the type-I, type-II, and N400m components which serve as snapshots of this process unfolding in the brain. For this model, we chose to focus on the early feed-forward processing occurring during visual word recognition, as the experimental setup in the MEG study was designed to demonstrate, rather than feed-back effects

[…]

By doing so, we restrict ourselves to an investigation of how well the three evoked components can be explained by a feed-forward CNN in an experimental setting designed to demonstrate feed-forward effects. > As such, the goal is not to present a complete model of all aspects of reading, which should include feed-back effects, but rather to demonstrate the effectiveness of using a model that has a realistic form of input when the aim is to align the model with the evoked responses observed during visual word recognition.”

And we have added the following to the Discussion section:

“In this paper we have restricted our simulations to feed-forward processes. Now, the way is open to incorporate convolution-and-pooling principles in models of reading that simulate feed-back processes as well, which should allow the model to capture more nuance in the Type-II and N400m components, as well as extend the simulation to encompass a realistic semantic representation. A promising way forward may be to use a network architecture like CORNet (Kubilius et al., 2019), that performs convolution multiple times in a recurrent fashion, yet simultaneously propagates activity forward after each pass. The introduction of recursion into the model will furthermore align it better with traditional-style models, since it can cause a model to exhibit attractor behavior (McLeod et al., 2000), which will be especially important when extending the model into the semantic domain.

Furthermore, convolution-and-pooling has recently been explored in the domain of predictive coding models (Ororbia & Mali, 2023), a type of model that seems particularly well suited to model feed-back processes during reading (Gagl et al., 2020; Heilbron et al., 2020; Nour Eddine et al., 2024).”

We also would like to point out to the Reviewer that we did in fact perform a correlation between the model and the MNE-dSPM source estimate of all cortical locations and timepoints (Figure 7B). Such a brain-wide correlation map confirms that the three dipole groups are excellent summaries of when and where interesting effects occur within this dataset.

The presented model needs substantial further development to be able to replicate, both behaviorally and neurally, many of the well-characterized phenomena seen in human behavior and neural recordings that are fundamental hallmarks of human visual word processing. Until that point, it is unclear what novel contributions can be gleaned from correlating low-dimensional model weights from these computational models with human neural data.

We hope that our revisions have clarified the goals and scope of this study. The CNN model we present in this study is a small but, we feel, essential piece in a bigger effort to employ deep learning techniques to further enhance already existing models of reading. In our revision, we have extended our discussion where to go from here and outline our vision on how these techniques could help us better model the phenomena the reviewer speaks of. We agree with the reviewer that there is a long way to go, and we are excited to be a part of it.

In addition to the changes described above, we now end the Discussion section as follows: 

“Despite its limitations, our model is an important milestone for computational models of reading that leverages deep learning techniques to encompass the entire computational process starting from raw pixels values to representations of wordforms in the mental lexicon. The overall goal is to work towards models that can reproduce the dynamics observed in brain activity observed during the large number of neuroimaging experiments performed with human volunteers that have been performed over the last few decades. To achieve this, models need to be able to operate on more realistic inputs than a collection of predefined lines or letter banks (for example: Coltheart et al., 2001; Heilbron et al., 2020; Laszlo & Armstrong, 2014; McClelland & Rumelhart, 1981; Nour Eddine et al., 2024). We have shown that even without feed-back connections, a CNN can simulate the behavior of three important MEG evoked components across a range of experimental conditions, but only if unit activations are noisy and the frequency of occurrence of words in the training dataset mimics their frequency of use in actual language.”

Reviewer #3 (Public Review):

The paper is rather qualitative in nature. In particular, the authors show that some resemblance exists between the behavior of some layers and some parts of the brain, but it is hard to quantitively understand how strong the resemblances are in each layer, and the exact impact of experimental settings such as the frequency balancing (which seems to only have a very moderate effect according to Figure 5).

The large focus on a qualitative evaluation of the model is intentional. The ability of the model to reproduce experimental effects (Figure 4) is a pre-requisite for any subsequent quantitative metrics (such as correlation) to be valid. The introduction of frequency balancing is a good example of this. As the reviewer points out, frequency balancing during training has only a moderate impact on correlation scores and from that point of view does not seem impactful. However, when we look at the qualitative evaluation, we see that with a large vocabulary, a model without frequency balancing fails to properly distinguish between consonant strings and (pseudo)words (Figure 4, 5th row). Hence, from the point of view of being able to reproduce experimental effects, frequency balancing has a large impact.

That said, the reviewer is right to highlight the value of quantitative analysis. An important limitation of the “traditional” models of reading that do not employ deep learning is that they operate in unrealistically simplified environments (e.g. input as predefined line segments, words of a fixed length), which makes a quantitative comparison with brain data problematic. The main benefit that deep learning brings may very well be the increase in scale that makes more direct comparisons with brain data possible. In our revision we attempt to capitalize on this benefit more. The reviewer has provided some helpful suggestions for doing so in their recommendations, which we discuss in detail below.

We have added the following discussion on the topic of qualitative versus quantitative analysis to the Introduction:

“We sought to construct a model that is able to recognize words regardless of length, size, typeface and rotation, as well as humans can, so essentially perfectly, whilst producing activity that mimics the type-I, type-II, and N400m components which serve as snapshots of this process unfolding in the brain.

[…]

These variations were first evaluated on their ability to replicate the experimental effects in that study, namely that the type-I response is larger for noise embedded words than all other stimuli, the type-II response is larger for all letter strings than symbols, and that the N400m is larger for real and pseudowords than consonant strings. Once a variation was found that could reproduce these effects satisfactorily, it was further evaluated based on the correlation between the amount of activation of the units in the model and MEG response amplitude.”

And follow this up in the Discussion with a new sub-section entitled “On the importance of experimental contrasts and qualitative analysis of the model”

The experiments only consider a rather outdated vision model (VGG).

VGG was designed to use a minimal number of operations (convolution-and-pooling, fullyconnected linear steps, ReLU activations, and batch normalization) and rely mostly on scale to solve the classification task. This makes VGG a good place to start our explorations and see how far a basic CNN can take us in terms of explaining experimental MEG effects in visual word recognition. However, we agree with the reviewer that it is easy to envision more advanced models that could potentially explain more. In our revision, we expand on the question of where to go from here and outline our vision on what types of models would be worth investigating and how one may go about doing that in a way that provides insights beyond higher correlation values.

We have included the following in our Discussion sub-sections on “Limitations of the current model and the path forward”:

“The VGG-11 architecture was originally designed to achieve high image classification accuracy on the ImageNet challenge (Simonyan & Zisserman, 2015). Although we have introduced some modifications that make the model more biologically plausible, the final model is still incomplete in many ways as a complete model of brain function during reading.

[…]

In this paper we have restricted our simulations to feed-forward processes. Now, the way is open to incorporate convolution-and-pooling principles in models of reading that simulate feed-back processes as well, which should allow the model to capture more nuance in the Type-II and N400m components, as well as extend the simulation to encompass a realistic semantic representation. A promising way forward may be to use a network architecture like CORNet (Kubilius et al., 2019), that performs convolution multiple times in a recurrent fashion, yet simultaneously propagates activity forward after each pass. The introduction of recursion into the model will furthermore align it better with traditional-style models, since it can cause a model to exhibit attractor behavior (McLeod et al., 2000), which will be especially important when extending the model into the semantic domain. Furthermore, convolution-and-pooling has recently been explored in the domain of predictive coding models (Ororbia & Mali, 2023), a type of model that seems particularly well suited to model feed-back processes during reading (Gagl et al., 2020; Heilbron et al., 2020; Nour Eddine et al., 2024).”

Reviewer #3 (Recommendations For The Authors):

(1) The method used to select the experimental conditions under which the behavior of the CNN is the most brain-like is rather qualitative (Figure 4). It would have been nice to have a plot where the noisyness of the activations, the vocab size and the amount of frequency balancing are varied continuously, and show how these three parameters impact the correlation of the model layers with the MEG responses.

We now include this analysis (Figure 6 in the revised manuscript, Supplementary Figures 47) and discuss these factors in the revised Results section:

“Various other aspects of the model architecture were evaluated which ultimately did not lead to any improvements of the model. The response profiles can be found in the supplementary information (Supplementary Figures 4–7) and the correlations between the models and the MEG components are presented in Figure 6. The vocabulary of the final model (10 000) exceeds the number of units in its fullyconnected layers, which means that a bottleneck is created in which a sub-lexical representation is formed. The number of units in the fully-connected layers, i.e. the width of the bottleneck, has some effect on the correlation between model and brain (Figure 6A), and the amount of noise added to the unit activations less so (Figure 6B). We already saw that the size of the vocabulary, i.e. the number of wordforms in the training data and number of units in the output layer of the model, had a large effect on the response profiles (Figure 4). Having a large vocabulary is of course desirable from a functional point of view, but also modestly improves correlation between model and brain (Figure 6C). For large vocabularies, we found it beneficial to apply frequency-balancing of the training data, meaning that the number of times a word-form appears in the training data is scaled according to its frequency in a large text corpus. However, this cannot be a one-to-one scaling, since the most frequent words occur so much more often than other words that the training data would consist of mostly the top-ten most common words, with less common words only occurring once or not at all. Therefore, we decided to scale not by the frequency 𝑓 directly, but by 𝑓𝑠, where 0 < 𝑠 < 1, opting for 𝑠 = 0.2 for the final model (Figure 6D).”

(2) It is not clear which layers exactly correspond to which of the three response components. For this to be clearer, it would have been nice to have a plot with all the layers of VGG on the x-axis and three curves corresponding to the correlation of each layer with each of the three response components.

This is a great suggestion that we were happy to incorporate in the revised version of the manuscript. Every figure comparing the response patterns of the model and brain now includes a panel depicting the correlation between each layer of the model and each of the three MEG components (Figures 4 & 5, Supplementary Figures 2-5). This has given us (and now also the reader) the ability to better benchmark the different models quantitatively, adding to our discussion on qualitative to quantitative analysis.

(3) It is not clear to me why the authors report the correlation of all layers with the MEG responses in Figure 5: why not only report the correlation of the final layers for N400, and that of the first layers for type-I?

We agree with the reviewer that it would have been better to compare the correlation scores for those layers which response profile matches the MEG component. While the old Figure 5 has been merged with Figure 4, and now provides the correlations between all the layers and all MEG components, we have taken the Reviewer’s advice and marked the layers which qualitatively best correspond to each MEG component, so the reader can take that into account when interpreting the correlation scores.

(4) The authors mention that the reason that they did not reproduce the protocol with more advanced vision models is that they needed the minimal setup capable of yielding the desired experiment effect. I am not fully convinced by this and think the paper could be significantly strengthened by reporting results for a vision transformer, in particular to study the role of attention layers which are expected to play an important role in processing higher-level features.

We appreciate and share the Reviewer’s enthusiasm in seeing how other model architectures would fare when it comes to modeling MEG components. However, we regard modifying the core model architecture (i.e., a series of convolution-and-pooling followed by fully-connected layers) to be out of scope for the current paper.

One of the key points of our study is to create a model that reproduces the experimental effects of an existing MEG study, which necessitates modeling the initial feed-forward processing from pixel to word-form. For this purpose, a convolution-and-pooling model was the obvious choice, because these operations play a big role in cognitive models of vision in general. In order to properly capture all experimental contrasts in the MEG study, many variations of the CNN were trained and evaluated. This iterative design process concluded when all experimental contrasts could be faithfully reproduced.

If we were to explore different model architectures, such as a transformer architecture, reproducing the experimental contrasts of the MEG study would no longer be the end goal, and it would be unclear what the end goal should be. Maximizing correlation scores has no end, and there are a nearly endless number of model architectures one could try. We could bring in a second MEG study with experimental contrasts that the CNN cannot explain and a transformer architecture potentially could and set the end goal to explain all experimental effects in both MEG studies. But even if we had access to such a dataset, this would almost double the length of the paper, which is already too long.

eLife Assessment

Hardly anything is known about the genetic basis and mechanism of male-killing. Recently, a gene called oscar, in the bacterium Wolbachia, was implicated in killing male corn borer moths by interfering with moth genes that control sex determination and proper dosage of sex-specific genes. In this paper, the authors show that a distantly related oscar gene in another strain of Wolbachia kills male tea tortrix moths in a similar mechanism. This valuable study cements our understanding of the sophisticated way that Wolbachia kills male moths and butterflies (Lepidoptera) so early in their development. The conclusions are supported by solid evidence.

Reviewer #1 (Public review):

Summary:

Insects and their relatives are commonly infected with microbes that are transmitted from mothers to their offspring. A number of these microbes have independently evolved the ability to kill the sons of infected females very early in their development; this male killing strategy has evolved because males are transmission dead-ends for the microbe. A major question in the field has been to identify the genes that cause male killing and to understand how they work. This has been especially challenging because most male-killing microbes cannot be genetically manipulated. This study focuses on a male-killing bacterium called Wolbachia. Different Wolbachia strains kill male embryos in beetles, flies, moths, and other arthropods. This is remarkable because how sex is determined differs widely in these hosts. Two Wolbachia genes have been previously implicated in male-killing by Wolbachia: oscar (in moth male-killing) and wmk (in fly male-killing). The genomes of some male-killing Wolbachia contain both of these genes, so it is a challenge to disentangle the two.

This paper provides strong evidence that oscar is responsible for male-killing in moths. Here, the authors study a strain of Wolbachia that kills males in a pest of tea, Homona magnanima. Overexpressing oscar, but not wmk, kills male moth embryos. This is because oscar interferes with masculinizer, the master gene that controls sex determination in moths and butterflies. Interfering with the masculinizer gene in this way leads the (male) embryo down a path of female development, which causes problems in regulating the expression of genes that are found on the sex chromosomes.

Strengths:

The authors use a broad number of approaches to implicate oscar, and to dissect its mechanism of male lethality. These approaches include: a) overexpressing oscar (and wmk) by injecting RNA into moth eggs, b) determining the sex of embryos by staining female sex chromosomes, c) determining the consequences of oscar expression by assaying sex-specific splice variants of doublesex, a key sex determination gene, and by quantifying gene expression and dosage of sex chromosomes, using RNASeq, and d) expressing oscar along with masculinizer from various moth and butterfly species, in a silkmoth cell line. This extends recently published studies implicating oscar in male-killing by Wolbachia in Ostrinia corn borer moths, although the Homona and Ostrinia oscar proteins are quite divergent. Combined with other studies, there is now broad support for oscar as the male-killing gene in moths and butterflies (i.e. order Lepidoptera).

Reviewer #2 (Public review):

Wolbachia are maternally transmitted bacteria that can manipulate host reproduction in various ways. Some Wolbachia induce male killing (MK), where the sons of infected mothers are killed during development. Several MK-associated genes have been identified in Homona magnanima, including Hm-oscar and wmk-1-4, but the mechanistic links between these Wolbachia genes and MK in the native host are still unclear.

In this manuscript, Arai et al. show that Hm-oscar is the gene responsible for Wolbachia-induced MK in Homona magnanima. They provide evidence that Hm-Oscar functions through interactions with the sex determination system. They also found that Hm-Oscar disrupts sex determination in male embryos by inducing female-type dsx splicing and impairing dosage compensation. Additionally, Hm-Oscar suppresses the function of Masc. The manuscript is well-written and presents intriguing findings. The results support their conclusions regarding the diversity and commonality of MK mechanisms, contributing to our understanding of the mechanisms and evolutionary aspects of Wolbachia-induced MK.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Insects and their relatives are commonly infected with microbes that are transmitted from mothers to their offspring. A number of these microbes have independently evolved the ability to kill the sons of infected females very early in their development; this male killing strategy has evolved because males are transmission dead-ends for the microbe. A major question in the field has been to identify the genes that cause male killing and to understand how they work. This has been especially challenging because most male-killing microbes cannot be genetically manipulated. This study focuses on a male-killing bacterium called Wolbachia. Different Wolbachia strains kill male embryos in beetles, flies, moths, and other arthropods. This is remarkable because how sex is determined differs widely in these hosts. Two Wolbachia genes have been previously implicated in male-killing by Wolbachia: oscar (in moth male-killing) and wmk (in fly male-killing). The genomes of some male-killing Wolbachia contain both of these genes, so it is a challenge to disentangle the two.

This paper provides strong evidence that oscar is responsible for male-killing in moths. Here, the authors study a strain of Wolbachia that kills males in a pest of tea, Homona magnanima. Overexpressing oscar, but not wmk, kills male moth embryos. This is because oscar interferes with masculinizer, the master gene that controls sex determination in moths and butterflies. Interfering with the masculinizer gene in this way leads the (male) embryo down a path of female development, which causes problems in regulating the expression of genes that are found on the sex chromosomes.

We would like to thank you for evaluating our manuscript.

Strengths:

The authors use a broad number of approaches to implicate oscar, and to dissect its mechanism of male lethality. These approaches include: a) overexpressing oscar (and wmk) by injecting RNA into moth eggs, b) determining the sex of embryos by staining female sex chromosomes, c) determining the consequences of oscar expression by assaying sex-specific splice variants of doublesex, a key sex determination gene, and by quantifying gene expression and dosage of sex chromosomes, using RNASeq, and d) expressing oscar along with masculinizer from various moth and butterfly species, in a silkmoth cell line. This extends recently published studies implicating oscar in male-killing by Wolbachia in Ostrinia corn borer moths, although the Homona and Ostrinia oscar proteins are quite divergent. Combined with other studies, there is now broad support for oscar as the male-killing gene in moths and butterflies (i.e. order Lepidoptera). So an outstanding question is to understand the role of wmk. Is it the master male-killing gene in insects other than Lepidoptera and if so, how does it operate?

We would like to thank you for evaluating our manuscript. Our data demonstrated that Oscar homologs play important roles in male-killing phenotypes in moths and butterflies; however, the functional relevance of wmk remains uncertain. As you noted, whether wmk acts as a male-killing gene in insects such as flies and beetles—or even in certain lepidopteran species—requires further investigation using diverse insect models, which we are eager to explore in future research.

Weaknesses:

I found the transfection assays of oscar and masculinizer in the silkworm cell line (Figure 4) to be difficult to follow. There are also places in the text where more explanation would be helpful for non-experts.

Thank you for your suggestion. We have revised the section on the cell-based experiment. Further, we revised the manuscript to make it accessible to a broader audience. We believe these revisions have significantly improved the clarity and comprehensiveness of our manuscript.

Reviewer #2 (Public review):

Summary:

Wolbachia are maternally transmitted bacteria that can manipulate host reproduction in various ways. Some Wolbachia induce male killing (MK), where the sons of infected mothers are killed during development. Several MK-associated genes have been identified in Homona magnanima, including Hm-oscar and wmk-1-4, but the mechanistic links between these Wolbachia genes and MK in the native host are still unclear.

In this manuscript, Arai et al. show that Hm-oscar is the gene responsible for Wolbachia-induced MK in Homona magnanima. They provide evidence that Hm-Oscar functions through interactions with the sex determination system. They also found that Hm-Oscar disrupts sex determination in male embryos by inducing female-type dsx splicing and impairing dosage compensation. Additionally, Hm-Oscar suppresses the function of Masc. The manuscript is well-written and presents intriguing findings. The results support their conclusions regarding the diversity and commonality of MK mechanisms, contributing to our understanding of the mechanisms and evolutionary aspects of Wolbachia-induced MK.

We would like to thank you for evaluating our manuscript.

Comments on revisions:

The authors have already addressed the reviewer's concerns.

We would like to thank you for evaluating our manuscript.

Reviewer #3 (Public review):

Summary:

Overall, this is a clearly written manuscript with nice hypothesis testing in a non-model organism that addresses the mechanism of Wolbachia-mediated male killing. The authors aim to determine how five previously identified male-killing genes (encoded in the prophage region of the wHm Wolbachia strain) impact the native host, Homona magnanima moths. This work builds on the authors' previous studies in which

(1) they tested the impact of these same wHm genes via heterologous expression in Drosophila melanogaster

(2) also examined the activity of other male-killing genes (e.g., from the wFur Wolbachia strain in its native host: Ostrinia furnacalis moths).

Advances here include identifying which wHm gene most strongly recapitulates the male-killing phenotype in the native host (rather than in Drosophila), and the finding that the Hm-Oscar protein has the potential for male-killing in a diverse set of lepidopterans, as inferred by the cell-culture assays.

We would like to thank you for evaluating our manuscript.

Strengths:

Strengths of the manuscript include the reverse genetics approaches to dissect the impact of specific male-killing loci, and use of a "masculinization" assay in Lepidopteran cell lines to determine the impact of interactions between specific masc and oscar homologs.

We would like to thank you for evaluating our manuscript.

Weaknesses:

It is clear from Figure 1 that the combinations of wmk homologs do not cause male killing on their own here. While I largely agree with the author's conclusions that oscar is the primary MK factor in this system, I don't think we can yet rule out that wmk(s) may work synergistically or interactively with oscar in vivo. This might be worth a small note in the discussion. (eg at line 294 'indicating that wmk likely targets factors other than masc." - this could be downstream of the impacts of oscar; perhaps dependent on oscar-mediated impacts on masc first).

We sincerely appreciate your suggestion. Whilst wmk genes themselves did not exhibit apparent lethal effects on the native host, as you noted, we cannot entirely rule out the possibility that wmk may be involved in male-killing actions, either directly or indirectly assisting the function of Hb-oscar. Following your suggestion, we have added a brief note in the discussion section regarding the interpretation of wmk functions.

“In addition, Katsuma et al. (2022) reported that the wmk homologs encoded by wFur did not affect the masculinizing function of masc in vitro, indicating that wmk likely targets factors other than masc. Whilst we cannot rule out the possibility that wmk may work synergistically or interactively with oscar in vivo—potentially acting downstream of oscar’s impact—our results strongly suggested that Wolbachia strains have acquired multiple MK genes through evolution.” (lines 287-292)

Regarding the perceived male-bias in Figure 2a: I think readers might be interpreting "unhatched" as "total before hatching". You could eliminate ambiguity by perhaps splitting the bars into male and female, and then within a bar, coloring by hatched versus unhatched. But this is a minor point, and I think the updated text helps clarify this.

Thank you for your suggestion. We have accordingly revised the figure 2a. In addition, we have included more detailed information in the first sentence of the section Males are killed mainly at the embryonic stage.

“The sex of hatched larvae (neonates) and the remaining unhatched embryos was determined by the presence or absence of W chromatin, a condensed structure of the female-specific W chromosome observed during interphase.” (lines 171-173)

The new Figure 4b looks to be largely redundant with the oscar information in Figure 1a.

Thank you for your suggestion. We have removed Figure 4b due to its overlap with Figure 1a and have incorporated relevant figure legends into the Figure 1a legend.

Updated statistical comparisons for the RNA-seq analysis are helpful. However these analyses are based on single libraries (albeit each a pool of many individuals), so this is still a weaker aspect of the manuscript.

Thank you for your suggestion. As you noted, the use of single libraries (due to the limited number of available individuals, though each includes approximately 50 males and females) may be a potential limitation of this study. However, as demonstrated in the qPCR assay for the Z-linked gene provided in the previous revision, we believe that our data and conclusion—that Wolbachia/ Hb-oscar disrupts dosage compensation by causing the overexpression of Z-linked genes—are well-supported and robust.

The new information on masc similarity is useful (Fig 4d) - if the authors could please include a heatmap legend for the colors, that would be helpful. Also, please avoid green and red in the same figure when key for interpretation.

Thank you for your suggestion. We have accordingly included a heatmap legend and revised the colors.

Figure 1A "helix-turn-helix" is misspelled. ("tern").

We have revised.

Recommendations for the authors:

Comments from the reviewing editor: I would suggest you address the comments of the reviewer on the revised version.

We have further revised the manuscript to address all the questions, comments and suggestions provided by the reviewers. We believe that the resulting revisions have significantly enhanced the quality and comprehensiveness of our manuscript.

Reviewer #1 (Recommendations for the authors):

Thank you for revising this manuscript. I have a few last recommendations:

- Line 214: re: 'Statistical data are available in the supplementary data file', it would be more helpful to add a few words here that actually summarize the statistical results

We would like to thank you for your suggestion. We have revised the sentence to describe the overview of the statistical results.

“RNA-seq analysis revealed that, in Hm-oscar-injected embryos, Z-linked genes (homologs on the B. mori chromosomes 1 and 15) were more expressed in males than in females (Fig. 3a), which was not observed in the GFP-injected group (Fig. 3b). Similarly, as previously reported by Arai et al. (2023a), high levels of Z-linked gene expression were also observed in wHm-t-infected males, but not in NSR males (Fig. 3c,d). The high (i.e., doubled) Z-linked gene expression in both Hm-oscar-expressed and wHm-t-infected males was further confirmed by quantification of the Z-linked Hmtpi gene (Fig. 3e). These trends were statistically supported, with all data available in the supplementary data file.” (lines 205-213)

- Figure 1 legend: do you mean 'bridged' instead of 'brigged'?

We have accordingly revise, thank you for the suggestion.

eLife Assessment

The authors have developed a biosensor for programmed cell death. They use this biosensor to provide cell death measurements in a specific early development time. The findings useful in a specific context; however, the application of this biosensor is incomplete as it does not take into account existing literature and is missing controls.

Joint Public Review:

Summary:

Jia and colleagues developed a fluorescence resonance energy transfer (FRET)-based biosensor to study programmed cell death in the zebrafish spinal cord. They applied this tool to study death of zebrafish spinal motor neurons.

Strengths:

Their analysis shows that the tool is a useful biosensor of motor neuron apoptosis in living zebrafish and can reveal which part of the neuron undergoes caspase activation first.

Weaknesses:

As far as it is possible to tell, the authors focus on death of motor neurons innervating axial muscles. Previous work from over 30 years ago revealed that only a small number of these motor neurons die early in development. So this is not new, although following the cells and learning details of their apoptosis is new. Most of the work on motor neuron death in tetrapods was carried out on limb innervating motor neurons. Zebrafish have paired pectoral and pelvic fins, homologs of tetrapod paired limbs. These fins are innervated by distinct sets of motor neurons in zebrafish, as they are in tetrapods. However, the authors have not focused on these particular motor neurons, and thus have not made a fair comparison with tetrapods. In fact, they do not tell us which spinal levels they observed or whether they have been consistent from animal to animal. Pelvic fins emerge much later than pectoral fins in zebrafish, so it is possible that the time frame during which the authors imaged motor neuron death does not include motor neurons innervating pelvic fins.

Author response:

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

Reviewer 1:

(1) The results do not support the conclusions. The main "selling point" as summarized in the title is that the apoptotic rate of zebrafish motorneurons during development is strikingly low (~2% ) as compared to the much higher estimate (~50%) by previous studies in other systems. The results used to support the conclusion are that only a small percentage (under 2%) of apoptotic cells were found over a large population at a variety of stages 24-120hpf. This is fundamentally flawed logic, as a short-time window measure of percentage cannot represent the percentage on the long-term. For example, at any year under 1% of human population die, but over 100 years >99% of the starting group will have died. To find the real percentage of motorneurons that died, the motorneurons born at different times must be tracked over long term, or the new motorneuron birth rate must be estimated. Similar argument can be applied to the macrophage results.<br />

In the revised manuscript (revised Figure 4), we extended the observation time window as long as possible, from 24 hpf to 240 hpf. After 240 hpf, the transparency of zebrafish body decreased dramatically, which made optical imaging quite difficult.

We are confident that this 24-240 hpf time window covers the major time window during which motor neurons undergo programmed cell death during zebrafish early development. We chose the observation time window based on the following two reasons: 1) Previous studies showed that although the time windows of motor neuron death vary in chick (E5-E10), mouse (E11.5-E15.5), rat (E15-E18), and human (11-25 weeks of gestation), the common feature of these time windows is that they are all the developmental periods when motor neurons contact with muscle cells. The contact between zebrafish motor neurons and muscle cells occurs before 72 hpf, which is included in our observation time window. 2) Most organs of zebrafish form before 48-72 hpf, and they complete hatching during 48-72 hpf. Food-seeking and active avoidance behaviors also start at 72 hpf, indicating that motor neurons are fully functional at 72 hpf.

Previous studies in zebrafish have shown that the production of spinal cord motor neurons largely ceases before 48 hpf, and then the motor neurons remain largely constant until adulthood (doi: 10.1016/j.celrep.2015.09.050; 10.1016/j.devcel.2013.04.012; 10.1007/BF00304606; 10.3389/fcell.2021.640414). Our observation time window covers the major motor neuron production process. Therefore, we believe that neurogenesis will not affect our findings and conclusions.

Although we are confident that 240 h tracking is long enough to measure the motor neuron death rate, several sentences have been added in the discussion part, “In our manuscript, we tracked the motor neuron death in live zebrafish until 240 hpf, which was the longest time window we could achieve. But there was still a possibility that zebrafish motor neurons might die after 240 hpf.”

We agreed that the “2%” description might not be very accurate. Thus, we have revised our title to “Zebrafish live imaging reveals a surprisingly small percentage of spinal cord motor neurons die during early development.”

(2) The conclusion regarding timing of axon and cell body caspase activation and apoptosis timing also has clear issues. The ~minutes measurement are too long as compared to the transport/diffusion timescale between the cell body and the axon, caspase activity could have been activated in the cell body and either caspase or the cleaved sensor move to the axon in several seconds. The authors' results are not high frequency enough to resolve these dynamics. Many statements suggest oversight of literature, for example, in abstract "however, there is still no real-time observation showing this dying process in live animals.".

Real-time imaging of live animals is quite challenging in the field. Currently, using confocal microscopy, we can only achieve minute-scale tracking. In the future, with more advanced imaging techniques, the sensor fish in the present study may provide us with more detailed information on motor neuron death. We have removed “real-time” from our revised manuscript. We also revised the mentioned sentence in the abstract.

(3) Many statements should use more scholarly terms and descriptions from the spinal cord or motorneuron, neuromuscular development fields, such as line 87 "their axons converged into one bundle to extend into individual somite, which serves as a functional unit for the development and contraction of muscle cells"

We have removed this sentence.

(4) The transgenic line is perhaps the most meaningful contribution to the field as the work stands. However, mnx1 promoter is well known for its non-specific activation - while the images do suggest the authors' line is good, motorneuron markers should be used to validate the line. This is especially important for assessing this population later as mnx1 may be turned off in mature neurons. The author's response regarding mnx1 specificity does not mitigate the original concern.

The mnx1 promoter has been widely used to label motor neurons in transgenic zebrafish. Previous studies have shown that most of the cells labeled in the mnx1 transgenic zebrafish are motor neurons. In this study, we observed that the neuronal cells in our sensor zebrafish formed green cell bodies inside of the spinal cord and extended to the muscle region, which is an important morphological feature of the motor neurons.

Furthermore, a few of those green cell bodies turned into blue apoptotic bodies inside the spinal cord and changed to blue axons in the muscle regions at the same time, which strongly suggests that those apoptotic neurons are not interneurons.

In fact, no matter what method is used, such as using antibodies to stain specific markers to label motor neurons, 100% specificity cannot be achieved. More importantly, although the mnx1 promoter might have labeled some interneurons, this will not affect our major finding that only a small percentage of spinal cord motor neurons die during the early development of zebrafish.

Reviewer 2:

(1) Title: The 50% figure of motor neurons dying through apoptosis during early vertebrate development is not precisely accurate. In papers referenced by the authors, there is a wide distribution of percentages of motor neurons that die depending on the species and the spinal cord region. In addition, the authors did not examine limb-innervating motor neurons, which are the ones best studied in motor neuron programmed cell death in other species. Thus, a better title that reflects what they actually show would be something like "A surprisingly small percentage of early developing zebrafish motor neurons die through apoptosis in non-limb innervating regions of the spinal cord."

In fish, there are no such structures as limbs, although fins may be evolutionarily related to limbs. In our manuscript, we studied the naturally occurring motor neuron death in the whole spinal cord during the early stage of zebrafish development. The death of motor neurons in limb-innervating motor neurons has been extensively studied in chicks and rodents, as it is easy to undergo operations such as amputation. However, previous studies have shown this dramatic motor neuron death occurs not only in limb-innervating motor neurons but also in other spinal cord motor neurons (doi: 10.1006/dbio.1999.9413).

We have revised our title to “Zebrafish live imaging reveals a surprisingly small percentage of spinal cord motor neurons die during early development.”

(2) lines 18-19: "embryonic stage of vertebrates" is very broad, since zebrafish are also vertebrates; it would be better to be more specific

lines 25-26: The authors should be more specific about which animals have widespread neuronal cell death.

We have revised our manuscript accordingly.

(3) lines 98-99; 110-111; 113; 122-123; 140-141: A cell can undergo apoptosis. But an axon, which is only part of a cell, cannot undergo apoptosis. Especially since the axon doesn't have a separate nucleus, and the definition of apoptosis usually includes nuclear fragmentation. A better subheading would describe the result, which is that caspase activation is seen in both the cell body and the axon.

We have revised the subheadings and related words in the manuscript accordingly. In the introduction, we also revised the expression of the third aim from “Which part of a neuron (cell body vs. axon) will die first?” to “Which part of a neuron (cell body vs. axon) will degrade first?”.

(4) lines 159-160; 178-179: This is an oversimplification of the literature. The authors should spell out which populations of motor neuron have been examined and say something about the similarities and difference in motor neuron death.

We have revised it accordingly.

(5) lines 200; 216: The authors did not observe macrophages engulfing motor neurons. But that does not mean that they cannot. Making the conclusion stated in this subheading would require some kind of experiment, not just observations.

We did observe few colocalizations of macrophages and dead motor neurons.  To more accurately express these data, in the revised manuscript, we used “colocalization” to replace “engulfment.” The subheading has been revised to “Most dead motor neurons were not colocalized with macrophages.” Accordingly, panel C of Figure 5 has also been revised.

(6) lines 234-246: The authors seem to have missed the point about VaP motor neuron death, which was two-fold. First, VaP death has been previously described, thus it could serve as a control for the work in this paper, especially since the conditions underlying VaP death and survival have been experimentally tested. Second, they should acknowledge that previous work showed that at least some motor neuron death in zebrafish differs from that described in chick and rodents. This conclusion came from work showing that death of VaP is independent of limitations in muscle innervation area, suggesting it is not coupled to muscle-derived neurotrophic factors.

Figures: The authors should say which level of the spinal cord they examined in each figure.

We have compared our findings with previous findings in the revised manuscript. The death of VaP motor neurons is not related to neurotrophic factors, but the death of other motor neurons may be related to neurotrophic factors, which needs further study and evidence. Our study examined the overall motor neuron apoptosis regardless of the causes and locations. To avoid misunderstanding, in the revised manuscript, we removed the data and words related to neurotrophic factors.

We also extended the observation time window as long as possible, from 24 hpf to 240 hpf (revised Figure 4). After 240 hpf, the transparency of zebrafish body decreased dramatically, which made the optical imaging quite difficult.

eLife Assessment

It is known from model organisms that genes' effects on traits are often modulated by environmental variables, but similar gene-by-environment (GxE) interactions have been difficult to detect using statistical analyses of genomic data, e.g., in humans. This study introduces a new framework to estimate gene-by-environment effects, treating it as a bias-variance tradeoff problem. The authors convincingly show that greater statistical power can be achieved in detecting GxE if an underlying model of polygenic GxE is assumed. This polygenic amplification model is a truly novel view with fundamental promise for the detection of GxE in genomic datasets, especially with continued development to detect more complex signals of amplification.

Reviewer #1 (Public review):

Experiments in model organisms have revealed that the effects of genes on heritable traits are often mediated by environmental factors -- so-called gene-by-environment (or GxE) interactions. In human genetics, however, where indirect statistical approaches must be taken to detect GxE, limited evidence has been found for pervasive GxE interactions. The present manuscript argues that the failure of statistical methods to detect GxE may be due to how GxE is modelled (or not modelled) by these methods.

The authors show, via re-analysis of an existing dataset in Drosophila, that a polygenic 'amplification' model can parsimoniously explain patterns of differential genetic effects across environments. (Work from the same lab had previously shown that the amplification model is consistent with differential genetic effects across the sexes for a number of traits in humans.) The parsimony of the amplification model allows for powerful detection of GxE in scenarios in which it pertains, as the authors show via simulation.

Before the authors consider polygenic models of GxE, however, they present a very clear analysis of a related question around GxE: When one wants to estimate the effect of an individual allele in a particular environment, when is it better to stratify one's sample by environment (reducing sample size, and therefore increasing the variance of the estimator) versus using the entire sample (including individuals not in the environment of interest, and therefore biasing the estimator away from the true effect specific to the environment of interest)? Intuitively, the sample-size cost of stratification is worth paying if true allelic effects differ substantially between the environment of interest and other environments (i.e., GxE interactions are large), but not worth paying if effects are similar across environments. The authors quantify this trade-off in a way that is both mathematically precise and conveys the above intuition very clearly. They argue on its basis that, when allelic effects are small (as in highly polygenic traits), single-locus tests for GxE may be substantially underpowered.

The paper is an important further demonstration of the plausibility of the amplification model of GxE, which, given its parsimony, holds substantial promise for the detection and characterization of GxE in genomic datasets. However, the empirical and simulation examples considered in the paper (and previous work from the same lab) are somewhat "best-case" scenarios for the amplification model, with only two environments and with these environments amplifying equally the effects of only a single set of genes. It would be an important step forward to demonstrate the possibility of detecting amplification in more complex scenarios, with multiple environments each differentially modulating the effects of multiple sets of genes. This could be achieved via simulations similar to those presented in the current manuscript.

Comments on revisions:

The authors have (with reasonable justification) said that my main recommendations for strengthening the conclusions of the paper are beyond its scope, and they have thoughtfully responded to my (and the other reviewer's) other comments. The paper is now more clearly written---in particular, the connection between the single-locus bias-variance tradeoff calculations and the polygenic results is much more transparent than before. Given that the authors have (again, with fair justification) chosen not to address my major comment, my broad assessment of the paper is unchanged---I think it is an important contribution to a critical topic---and I have no further comments for its improvement (though I note an issue with figure referencing in the captions of Supplementary Figs S2 and S3).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Experiments in model organisms have revealed that the effects of genes on heritable traits are often mediated by environmental factors---so-called gene-by-environment (or GxE) interactions. In human genetics, however, where indirect statistical approaches must be taken to detect GxE, limited evidence has been found for pervasive GxE interactions. The present manuscript argues that the failure of statistical methods to detect GxE may be due to how GxE is modelled (or not modelled) by these methods.

The authors show, via re-analysis of an existing dataset in Drosophila, that a polygenic ‘amplification’ model can parsimoniously explain patterns of differential genetic effects across environments. (Work from the same lab had previously shown that the amplification model is consistent with differential genetic effects across the sexes for several traits in humans.) The parsimony of the amplification model allows for powerful detection of GxE in scenarios in which it pertains, as the authors show via simulation.

Before the authors consider polygenic models of GxE, however, they present a very clear analysis of a related question around GxE: When one wants to estimate the effect of an individual allele in a particular environment, when is it better to stratify one’s sample by environment (reducing sample size, and therefore increasing the variance of the estimator) versus using the entire sample (including individuals not in the environment of interest, and therefore biasing the estimator away from the true effect specific to the environment of interest)? Intuitively, the sample-size cost of stratification is worth paying if true allelic effects differ substantially between the environment of interest and other environments (i.e., GxE interactions are large), but not worth paying if effects are similar across environments. The authors quantify this trade-off in a way that is both mathematically precise and conveys the above intuition very clearly. They argue on its basis that, when allelic effects are small (as in highly polygenic traits), single-locus tests for GxE may be substantially underpowered.

The paper is an important further demonstration of the plausibility of the amplification model of GxE, which, given its parsimony, holds substantial promise for the detection and characterization of GxE in genomic datasets. However, the empirical and simulation examples considered in the paper (and previous work from the same lab) are somewhat “best-case” scenarios for the amplification model, with only two environments, and with these environments amplifying equally the effects of only a single set of genes. It would be an important step forward to demonstrate the possibility of detecting amplification in more complex scenarios, with multiple environments each differentially modulating the effects of multiple sets of genes. This could be achieved via simulations similar to those presented in the current manuscript.

Reviewer #2 (Public Review):

Summary:

Wine et al. describe a framework to view the estimation of gene-context interaction analysis through the lens of bias-variance tradeoff. They show that, depending on trait variance and context-specific effect sizes, effect estimates may be estimated more accurately in context-combined analysis rather than in context-specific analysis. They proceed by investigating, primarily via simulations, implications for the study or utilization of gene-context interaction, for testing and prediction, in traits with polygenic architecture. First, the authors describe an assessment of the identification of context-specificity (or context differences) focusing on “top hits” from association analyses. Next, they describe an assessment of polygenic scores (PGSs) that account for context-specific effect sizes, showing, in simulations, that often the PGSs that do not attempt to estimate context-specific effect sizes have superior prediction performance. An exception is a PGS approach that utilizes information across contexts. Strengths:

The bias-variance tradeoff framing of GxE is useful, interesting, and rigorous. The PGS analysis under pervasive amplification is also interesting and demonstrates the bias-variance tradeoff.

Weaknesses:

The weakness of this paper is that the first part -- the bias-variance tradeoff analysis -- is not tightly connected to, i.e. not sufficiently informing, the later parts, that focus on polygenic architecture. For example, the analysis of “top hits” focuses on the question of testing, rather than estimation, and testing was not discussed within the bias-variance tradeoff framework. Similarly, while the PGS analysis does demonstrate (well) the bias-variance tradeoff, the reader is left to wonder whether a bias-variance deviation rule (discussed in the first part of the manuscript) should or could be utilized for PGS construction.

We thank the editors and the reviewers for their thoughtful critique and helpful suggestions throughout. In our revision, we focused on tightening the relationship between the analytical single variant bias-variance tradeoff derivation and the various empirical analyses that follow.

We improved discussion of our scope and what is beyond our scope. For example, our language was insufficiently clear if it suggested to the editor and reviewers that we are developing a method to characterize polygenic GxE. Developing a new method that does so (let alone evaluating performance across various scenarios) is beyond the scope of this manuscript.

Similarly, we clarify that we use amplification only as an example of a mode of GxE that is not adequately characterized by current approaches. We do not wish to argue it is an omnibus explanation for all GxE in complex traits. In many cases, a mixture of polygenic GxE relationships seems most fitting (as observed, for example, in Zhu et al., 2023, for GxSex in human physiology).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

MAJOR COMMENT

The amplification model is based on an understanding of gene networks in which environmental variables concertedly alter the effects of clusters of genes, or modules, in the network (e.g., if an environmental variable alters the effect of some gene, it indirectly and proportionately alters the effects of genes downstream of that gene in the network---or upstream if the gene acts as a bottleneck in some pathway). It is clear in this model that (i) multiple environmental variables could amplify distinct modules, and (ii) a single environmental variable could itself amplify multiple separate modules, with a separate amplification factor for each module.

However, perhaps inspired by their previous work on GxSex interactions in humans, the authors’ focus in the present manuscript is on cases where there are only two environments (“control” and “high-sugar diet” in the Drosophila dataset that they reanalyze, and “A” and “B” in their simulations [and single-locus mathematical analysis]), and they consider models where these environments amplify only a single set of genes, i.e., with a single amplification factor. While it is of course interesting that a single-amplification-factor model can generate data that resemble those in the Drosophila dataset that the authors re-analyze, most scenarios of amplification GxE will presumably be more complex. It seems that detecting amplification in these more complex scenarios using methods such as the authors do in their final section will be correspondingly more difficult. Indeed, in the limit of sufficiently many environmental variables amplifying sufficiently many modules, the scenario would resemble one of idiosyncratic single-locus GxE which, as the authors argue, is very difficult to detect. That more complex scenarios of amplification, with multiple environments separately amplifying multiple modules each, might be difficult to detect statistically is potentially an important limitation to the authors’ approach, and should be tested in their simulations.

We agree that characterizing GxE when there is a mixture of drivers of context-dependency is difficult. Developing a method that does so across multiple (and perhaps not pre-defined) contexts is of high interest to us but beyond the scope of the current manuscript

We note that for GxSex, modeling this mixture does generally improve phenotypic prediction, and more so in traits where we infer amplification as a major mode of GxE.

MINOR COMMENTS

Lines 88-90: “This estimation model is equivalent to a linear model with a term for the interaction between context and reference allele count, in the sense that context-specific allelic effect estimators have the same distributions in the two models.”

Does this equivalence require the model with the interaction term also to have an interaction term for the intercept, i.e., the slope on a binary variable for context (since the generative model in Eq. 1 allows for context-specific intercepts)?

It does require an interaction term for the intercept. This is e_i (and its effect beta_E) in Eq. S2 (line 70 of the supplement).

Lines 94-96: Perhaps just a language thing, but in what sense does the estimation model described in lines 92-94 “assume” a particular distribution of trait values in the combined sample? It’s just an OLS regression, and one can analyze its expected coefficients with reference to the generative model in Eq. 1, or any other model. To say that it “assumes” something presupposes its purpose, which is not clear from its description in lines 92-94.

We corrected “assume” to “posit”.

Lines 115-116: It should perhaps be noted that the weights wA and wB need not sum to 1.

Indeed; it is now explicitly stated.

Lines 154-160: I think the role of r could be made even clearer by also discussing why, when VA>>VB, it is better to use the whole-sample estimate of betaA than the sample-A-specific estimate (since this is a more counterintuitive case than the case of VA<<VB discussed by the authors).

This is addressed in lines 153-154, stating: “Typically, this (VA<<VB) will also imply that the additive estimator is greatly preferable for estimating β_B , as β_B will be extremely noisy”

Line 243 and Figure 4 caption: The text states that the simulated effects in the high-sugar environment are 1.1x greater than those in the control environment, while the caption states that they are 1.4x greater.

We have corrected the text to be consistent with our simulations.

TYPOS/WORDING

Line 14: “harder to interpret” --> “harder-to-interpret”

Line 22: We --> we

Line 40: “as average effect” -> “as the average effect”?

Line 57: “context specific” --> “context-specific”

Line 139: “re-parmaterization” --> “re-parameterization”

Lines 140, 158, 412: “signal to noise” --> “signal-to-noise”

Figure 3C,D: “pule rate” --> “pulse rate”

The caption of Figure 3: “conutinous” --> “continuous”

Line 227: “a variant may fall” --> “a variant may fall into”

Line 295: “conferring to more GxE” --> “conferring more GxE” or “corresponding to more GxE”? This is very pedantic, but I think “bias-variance” should be “bias--variance” throughout, i.e., with an en-dash rather than a hyphen.

We have corrected all of the above typos.

Reviewer #2 (Recommendations For The Authors):

(This section repeats some of what I wrote earlier).

- First polygenic architecture part: the manuscript focuses on “top hits” in trying to identify sets of variants that are context-specific. This “top hits” approach seems somewhat esoteric and, as written, not connected tightly enough to the bias-variance tradeoff issue. The first section of the paper which focuses on bias-variance trade-off mostly deals with estimation. The “top hits” section deals with testing, which introduces additional issues that are due to thresholding. Perhaps the authors can think of ways to make the connection stronger between the bias-variance tradeoff part to the “top hits” part, e.g., by introducing testing earlier on and/or discussion estimation in addition to testing in the “top hits” part of the manuscript. The second polygenic architecture part: polygenic scores that account for interaction terms. Here the authors focused (well, also here) on pervasive amplification in simulations. This part combines estimation and testing (both the choice of variants and their estimated effects are important). In pervasive amplification the idea is that causal variants are shared, the results may be different than in a model with context-specific effects and variant selection may have a large impact. Still, I think that these simulations demonstrate the idea developed in the bias-variance tradeoff part of the paper, though the reader is left to wonder whether a bias-variance decision rule should or could be utilized for PGS construction.

In both of these sections we discuss how the consideration of polygenic GxE patterns alters the conclusions based on the single-variant tradeoff. In the “top hits” section, we show that single-variant classification itself, based on a series of marginal hypothesis tests alone, can be misleading. The PGS prediction accuracy analysis shows that both approaches are beaten by the polygenic GxE estimation approach. Intuitively, this is because the consideration of polygenic GxE can mitigate both the bias and variance, as it leverages signals from many variants.

We agree that the links between these sections of the paper were not sufficiently clear, and have added signposting to help clarify them (lines 176-180; lines 275-277; lines 316-321).

- Simulation of GxDiet effects on longevity: the methods of the simulation are strange, or communicated unclearly. The authors’ report (page 17) poses a joint distribution of genetic effects (line 439), but then, they simulated effect estimates standard errors by sampling from summary statistics (line 445) rather than simulated data and then estimating effect and effect SE. Why pose a true underlying multivariate distribution if it isn’t used?

We rewrote the Methods section “Simulation of GxDiet effects on longevity in Drosophila to make our simulation approach clearer (lines 427-449). We are indeed simulating the true effects from the joint distribution proposed. However, in order to mimic the noisiness of the experiment in our simulations, we sample estimated effects from the true simulated effects, with estimation noise conferring to that estimated in the Pallares et al. dataset (i.e., sampling estimation variances from the squares of empirical SEs).

- How were the “most significantly associated variants” selected into the PGS in the polygenic prediction part? Based on a context-specific test? A combined-context test of effect size estimates?

For the “Additive” and “Additive ascertainment, GxE estimation” models (red and orange in Fig. 5, respectively), we ascertain the combined-context set. For the “GxE” and “polygenic GxE” (green and blue in Fig. 5, respectively) models, we ascertain in a context-specific test. We now state this explicitly in lines 280-288 and lines 507-526.

- As stated, I find the conclusion statement not specific enough in light of the rest of the manuscript. “the consideration of polygenic GxE trends is key” - this is very vague. What does it mean “to consider polygenic GxE trends” in the context of this paper? I can’t tell. “The notion that complex trait analyses should combine observations at top associated loci” - I don’t think the authors really refer to combining “observations”, rather perhaps combine information from top associated loci. But this does not represent the “top hits” approach that merely counts loci by their testing patterns. “It may be a similarly important missing piece...” What does “it” refer to? The top loci? What makes it an important missing piece?

We rewrote the conclusion paragraph to address these concerns (lines 316-321).

eLife Assessment

This important study reports numerous attempts to replicate reports on transgenerational inheritance of a learned behavior – pathogen avoidance – in C. elegans. While the authors observe parental effects that are limited to a single generation (also called intergenerational inheritance), the authors failed to find evidence for transmission over multiple generations, or transgenerational inheritance. The experiments presented are meticulously described, making for compelling evidence that in the authors' hands transgenerational inheritance cannot be observed. There remains the possibility that different assay setups explain the failure to reproduce previous observations, although the authors present data suggesting that details of the assay are not that significant. There also remains the possibility that differences in culture conditions or lab environment explain the failure to reproduce previous observations, with updates to the paper having further reduced the probability that this applies here. Even if this were the case, it would imply that the original experimental paradigm was dependent on a very specific context. Given the prominence of the original reports of transgenerational inheritance, the present study is of broad interest to anyone studying genetics, epigenetics, or learned behavior.

[As also pointed out by the authors of this study, the authors of the original reports have provided a response on bioRxiv (DOI: https://doi.org/10.1101/2025.01.21.634111).]

Reviewer #1 (Public review):

Summary:

The authors report an inability to reproduce a transgenerational memory of avoidance of the pathogen PA14 in C. elegans. Instead, the authors demonstrate intergenerational inheritance for a single F1 generation, in embryos of mothers exposed to OP50 and PA14, where embryos isolated from these mothers by bleaching are capable of remembering to avoid PA14 in a manner that is dependent on systemic RNAi proteins sid-1 and sid-2. This could reflect systemic sRNAs generated by neuronal daf-7 signaling that are transmitted to F1 embryos. The authors note that transgenerational memory of PA14 was reported by the Murphy group at Princeton, but that environmental or strain variation (worms or bacteria) might explain the single generation of inheritance observed at Harvard. The Hunter group tried different bacterial growth conditions and different worm growth temperatures for independent PA14 strains, which they show to be strongly pathogenic. However, the authors could not reproduce a transgenerational effect at Harvard. This paper honestly alters expectations and indicates that the model that avoidance of PA14 is remembered for multiple generations is not robust enough to be replicated in all laboratories.

Overall, this paper that demonstrates that one model for transgenerational inheritance in C. elegans is not robust. The author do demonstrate an avoidance memory for F1 embryos that could be a maternal effect, and the authors confirm that this is mediated by a systemic small RNA response. There are several points in the manuscript where a more positive tone might be helpful.

Strengths:

The authors note that the high copy number daf-7::GFP transgene used by the Murphy group displayed variable expression and evidence for somatic silencing or transgene breakdown in the Hunter lab, as confirmed by the Murphy group. The authors nicely use single copy daf-7::GFP to show that neuronal daf-7::GFP is elevated in F1 but not F2 progeny with regards to memory of PA14 avoidance, speaking to an intergenerational phenotype.

The authors nicely confirm that sid-1 and sid-2 are generally required for intergenerational avoidance of F1 embryos of moms exposed to PA14. However, these small RNA proteins did not affect daf-7::GFP elevation in the F1 progeny. This result is unexpected given previous reports that daf-7::GFP is not elevated in F1 progeny of sid mutants.

The authors studied antisense small RNAs that change in Murphy data sets, identifying 116 mRNAs that might be regulated by sRNAs in response to PA14. The authors show that the maco-1 gene, putatively targeted by piRNAs according to the Kaletsky 2020 paper, displays few siRNAs that change in response to PA14. The authors conclude that the P11 ncRNA of PA14, which was proposed to promote interkingdom RNA communication by the Murphy group, may not affect maco-1 expression in C. elegans, although they did not formally demonstrate this. The authors define 8 genes based on their analysis of sRNAs and mRNAs that might promote resistance to PA14, but they do not further characterize these genes' role in pathogen avoidance. Others might wish to consider following up on these genes and their possible relationship with P11.

Weaknesses:

This very thorough and interesting manuscript is at times pugnacious.

Please explain more clearly what is High Growth media for E. coli in the text and methods, conveying why it was used by the Murphy lab, and if Normal Growth or High Growth is better for intergenerational heritability assays.

Comments on revisions:

The authors have done a reasonable job cordially revising this manuscript, and the authors have addressed most reviewer concerns. It is likely that the P11 gene was in some of the PA14 Pseudomonas strains tested, as one was kindly provided by the Murphy group.

Reviewer #2 (Public review):

This paper examines the reproducibility of results reported by the Murphy lab regarding transgenerational inheritance of a learned avoidance behavior in C. elegans. It has been well established by multiple labs that worms can learn to avoid the pathogen pseudomonas aeruginosa (PA14) after a single exposure. The Murphy lab has reported that learned avoidance is transmittable to 4 generations and dependent on a small RNA expressed by PA14 that elicits the transgenerational silencing of a gene in C. elegans. The Hunter lab now reports that although they can reproduce inheritance of the learned behavior by the first generation (F1), they cannot reproduce inheritance in subsequent generations.

This is an important study that will be useful for the community. Although they fail to identify a "smoking gun", the study examine several possible sources for the discrepancy, and their findings will be useful to others interested in using these assays. The preference assay appears to work in their hands in as much as they are able to detect the learned behavior in the P0 and F1 generations, suggesting that the failure to reproduce the transgenerational effect is not due to trivial mistakes in the protocol. The authors provide a full protocol and highlight key deviations from the Murphy lab protocol. The authors provide good evidence that no single protocol modification was sufficient on its own to explain the divergent results. It remains possible that protocol differences affected the assay cumulatively or that other uncontrolled factors were responsible. Nevertheless, the authors provide good evidence that the trans-generational effect reported by the Murphy lab lacks experimental robustness, calling into question its ecological relevance in the wild.

Reviewer #3 (Public review):

Summary:

It has been previously reported in many high-profile papers, that C. elegans can learn to avoid pathogens. Moreover, this learned pathogen avoidance can be passed on to future generations - up to the F5 generation in some reports. In this paper, Gainey et al. set out to replicate these findings. They successfully replicated pathogen avoidance in the exposed animals, as well as a strong increase in daf-7 expression in ASI neurons in F1 animals, as determined by a daf-7::GFP reporter construct. However, they failed to see strong evidence for pathogen avoidance or daf-7 overexpression in the F2 generation. The failure of replication is the major focus of this work.<br /> Given their failure to replicate these findings, the authors embark on a thorough test of various experimental confounders that may have impacted their results. They also re-analyze the small RNA sequencing and mRNA sequencing data from one of the previously published papers and draw some new conclusions, extending this analysis.

Strengths:

• The authors provide a thorough description of their methods, and a marked-up version of a published protocol that describes how they adapted the protocol to their lab conditions. It should be easy to replicate the experiments.

• The authors test source of bacteria, growth temperature (of both C. elegans and bacteria), and light/dark husbandry conditions. They also supply all their raw data, so that sample size for each testing plate can be easily seen (in the supplementary data). None of these variations appears to have a measurable effect on pathogen avoidance in the F2 generation, with all but one of the experiments failing to exhibit learned pathogen avoidance.

• The small RNA seq and mRNA seq analysis is well performed and extends the results shown in the original paper. The original paper did not give many details of the small RNA analysis, which was an oversight. Although not a major focus of this paper, it is a worthwhile extension on the previous work.

• It is rare that negative results such as these are accessible. Although the authors were unable to determine the reason that their results differ from those previously published, it is important to document these attempts in detail, as has been done here. Behavioral assays are notoriously difficult to perform and public discourse around these attempts may give clarity to the difficulties faced by a controversial field.

Weaknesses:

• Although the "standard" conditions have been tested over multiple biological replicates, many of the potential confounders that may have altered the results have been tested only once or twice. For example, changing the incubation temperature to 25{degree sign}C was tested in only two biological replicates (Exp 5.1 and 5.2) - and one of these experiments actually resulted in apparent pathogen avoidance inheritance in the F2 generation (but not in the F1). An alternative pathogen source was tested in only one biological replicate (Exp 3). Given the variability observed in the F2 generation, increasing biological replicates would have added to the strengths of the report.

• A key difference between the methods used here and those published previously, is an increase in the age of the animals used for training - from mostly L4 to mostly young adults. I was unable to find a clear example of an experiment when these two conditions were compared, although the authors state that it made no difference to their results.

• The original paper reports a transgenerational avoidance effect up to the F5 generation. Although in this work the authors failed to see avoidance in the F2 generation, it would have been prudent to extend their tests for more generations in at least a couple of their experiments to ensure that the F2 generation was not an aberration (although this reviewer acknowledges that this seems unlikely to be the case).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

[…] Overall, this is an important paper that demonstrates that one model for transgenerational inheritance in C. elegans is not reproducible. This is important because it is not clear how many of the reported models of transgenerational inheritance reported in C. elegans are reproducible. The authors do demonstrate a memory for F1 embryos that could be a maternal effect, and the authors confirm that this is mediated by a systemic small RNA response. There are several points in the manuscript where a more positive tone might be helpful.

We would like to correct the statement made in the second to last sentence. The demonstration of an F1 response to PA14 was first reported by Moore et al., (2019) and then by Pereira et al., (2020) using a different behavioral assay. We merely confirmed these results in our hands, and confirmed the observation, first reported by Kaletsky et al., (2020), that sid-1 and sid-2 are required for this F1 response; although we did find that sid-1 and sid-2 are not required for the PA14-induced increase in daf-7p::gfp expression in ASI neurons in the F1 progeny of trained adults, which had not been addressed in the published work.

Yes, the intergenerational F1 response could be a maternal effect, but the in utero F1 embryos and their precursor germ cells were directly exposed to PA14 metabolites and toxins (non-maternal effect) as well as any parental response, whether mediated by small RNAs, prions, hormones, or other unknown information carriers. While the F1 aversion response does require sid-1 and sid-2, we would not presume that the substrate is therefore an RNA molecule, particularly because the systemic RNAi response supported by sid-1 and sid-2 is via long double-stranded RNA. To date, no evidence suggests that either protein transports small RNAs, particularly single-stranded RNAs.

Strengths:

The authors note that the high copy number daf-7::GFP transgene used by the Murphy group displayed variable expression and evidence for somatic silencing or transgene breakdown in the Hunter lab, as confirmed by the Murphy group. The authors nicely use single copy daf-7::GFP to show that neuronal daf-7::GFP is elevated in F1 but not F2 progeny with regards to the memory of PA14 avoidance, speaking to an intergenerational phenotype.

The authors nicely confirm that sid-1 and sid-2 are generally required for intergenerational avoidance of F1 embryos of moms exposed to PA14. However, these small RNA proteins did not affect daf-7::GFP elevation in the F1 progeny. This result is unexpected given previous reports that single copy daf-7::GFP is not elevated in F1 progeny of sid mutants. Because the Murphy group reported that daf-7 mutation abolishes avoidance for F1 progeny, this means that the sid genes function downstream of daf-7 or in parallel, rather than upstream as previously suggested.

The published report (Moore et al., 2019) shows only multicopy daf-7p::gfp results and does not address the daf-7p::gfp response in sid-1 or sid-2 mutants. Thus, our discovery that systemic RNAi, exogenous RNAi, and heritable RNAi mutants don’t disrupt elevated daf-7p::gfp in ASI neurons in the F1 progeny of PA14 trained P0’s is only unexpected with respect to the published models (Moore et al., 2019, Kaletsky et al., 2020).

The authors studied antisense small RNAs that change in Murphy data sets, identifying 116 mRNAs that might be regulated by sRNAs in response to PA14. Importantly, the authors show that the maco-1 gene, putatively targeted by piRNAs according to the Kaletsky 2020 paper, displays few siRNAs that change in response to PA14. The authors conclude that the P11 ncRNA of PA14, which was proposed to promote interkingdom RNA communication by the Murphy group, is unlikely to affect maco-1 expression by generating sRNAs that target maco-1 in C. elegans. The authors define 8 genes based on their analysis of sRNAs and mRNAs that might promote resistance to PA14, but they do not further characterize these genes' role in pathogen avoidance. The Murphy group might wish to consider following up on these genes and their possible relationship with P11.

Weaknesses:

This very thorough and interesting manuscript is at times pugnacious.

We reiterate that we never claimed that Moore et al., (2019) did not obtain their reported results. We simply stated that we could not replicate their results using the published methods and then failed in our search to identify variable(s) that might account for our results. In revising the manuscript, we have striven to make clear, unmuddied statements of facts and state that future investigations may provide independent evidence that supports the original claims and explains our divergent results.

Please explain more clearly what is High Growth media for E. coli in the text and methods, conveying why it was used by the Murphy lab, and if Normal Growth or High Growth is better for intergenerational heritability assays.

We added the standard recipes and the following explanations in the methods section to the revised text.

“NG plates minimally support OP50 growth, resulting in a thin lawn that facilitates visualization of larvae and embryos. HG plates (8X more peptone) support much higher OP50 growth, resulting in a thick bacterial lawn that supports larger worm populations.”

We have also included the following text in our presentation and discussion of the effects of growth conditions on worm choice in PA14 vs OP50 choice assays.

“Furthermore, because OP50 pathogenicity is enhanced by increased E. coli nutritive conditions (Garsin et al., 2003, Shi et al., 2006), the growth of F1-F4 progeny on High Growth (HG) plates (Moore et al., 2019; 2021b), which contain 8X more peptone than NG plates and therefore support much higher OP50 growth levels, immediately prior to the F1-F4 choice assays may further contribute to OP50 aversion among the control animals.”

We don’t know enough to claim that HG or NG media is better than the other for intergenerational assays, but they are different. Thus, switching between the two in a multigenerational experiment likely introduces unknown variability.

Reviewer #2 (Public Review):

This paper examines the reproducibility of results reported by the Murphy lab regarding transgenerational inheritance of a learned avoidance behavior in C. elegans. It has been well established by multiple labs that worms can learn to avoid the pathogen pseudomonas aeruginosa (PA14) after a single exposure. The Murphy lab has reported that learned avoidance is transmittable to 4 generations and dependent on a small RNA expressed by PA14 that elicits the transgenerational silencing of a gene in C. elegans. The Hunter lab now reports that although they can reproduce inheritance of the learned behavior by the first generation (F1), they cannot reproduce inheritance in subsequent generations.

This is an important study that will be useful for the community. Although they fail to identify a "smoking gun", the study examines several possible sources for the discrepancy, and their findings will be useful to others interested in using these assays. The preference assay appears to work in their hands in as much as they are able to detect the learned behavior in the P0 and F1 generations, suggesting that the failure to reproduce the transgenerational effect is not due to trivial mistakes in the protocol. An obvious reason, however, to account for the differing results is that the culture conditions used by the authors are not permissive for the expression of the small RNA by PA14 that the MUrphy lab identified as required for transgenerational inheritance. It would seem prudent for the authors to determine whether this small RNA is present in their cultures, or at least acknowledge this possibility.

We thank the reviewer for raising this issue and have added the following statement to this effect in the revised manuscript.

“We note that previous bacterial RNA sequence analysis identified a small non-coding RNA called P11 whose expression correlates with bacterial growth conditions that induce heritable avoidance (Kaletsky et al., 2020). Critically, C. elegans trained on a PA14 ΔP11 strain (which lacks this small RNA) still learn to avoid PA14, but their F1 and F2-F4 progeny fail to show an intergenerational or transgenerational response (Figure 3L in Kaletsky et al., 2020). The fact that we observed an intergenerational (F1) avoidance response is evidence that our PA14 growth conditions induce P11 expression.”

We believe that this addresses the concern raised here.

The authors should also note that their protocol was significantly different from the Murphy protocol (see comments below) and therefore it remains possible that protocol differences cumulatively account for the different results.

As suggested below, we have added to the supplemental documents the protocol we followed for the aversion assay. In our view, this document shows that our adjustments to the core protocol were minor. Furthermore, where possible, these adjustments were explicitly tested in side-by-side experiments for both the aversion assay and the daf-7p::gfp expression assay and presented in the manuscript.

To discover the source(s) of discrepancy between our results and the published results we subsequently introduced variations to this core protocol to exclude likely variables (worm and bacteria growth temperatures, assay conditions, worm handling methods, bacterial culture and storage conditions, and some minor developmental timing issues). Again, where possible, the effect of variations was tested in side-by-side experiments for both the aversion assay and the daf-7p::gfp expression assay and were presented in or have now been added to the manuscript.

It remains possible that we misunderstood the published Murphy lab protocols, but we were highly motivated to replicate the results so we could use these assays to investigate the reported RNAi-pathway dependent steps, thus we read every published version with extreme care.

Reviewer #3 (Public Review):

[…] Strengths:

(1) The authors provide a thorough description of their methods, and a marked-up version of a published protocol that describes how they adapted the protocol to their lab conditions. It should be easy to replicate the experiments.

As noted above in response to a suggestion by reviewer #2, we have replaced the annotated published protocol with the protocol that we followed. This will aid other groups' attempts to replicate our experimental conditions.

(2) The authors test the source of bacteria, growth temperature (of both C. elegans and bacteria), and light/dark husbandry conditions. They also supply all their raw data, so that the sample size for each testing plate can be easily seen (in the supplementary data). None of these variations appears to have a measurable effect on pathogen avoidance in the F2 generation, with all but one of the experiments failing to exhibit learned pathogen avoidance.

We note that the parallel analysis of daf-7p::gfp expression in ASI neurons was also tested for several of these conditions and also failed to replicate the published findings.

(3) The small RNA seq and mRNA seq analysis is well performed and extends the results shown in the original paper. The original paper did not give many details of the small RNA analysis, which was an oversight. Although not a major focus of this paper, it is a worthwhile extension of the previous work.

(4) It is rare that negative results such as these are accessible. Although the authors were unable to determine the reason that their results differ from those previously published, it is important to document these attempts in detail, as has been done here. Behavioral assays are notoriously difficult to perform and public discourse around these attempts may give clarity to the difficulties faced by a controversial field.

Thank you for your support. Choosing to pursue publication of these negative results was not an easy decision, and we thank members of the community for their support and encouragement.

Weaknesses:

(1) Although the "standard" conditions have been tested over multiple biological replicates, many of the potential confounders that may have altered the results have been tested only once or twice. For example, changing the incubation temperature to 25{degree sign}C was tested in only two biological replicates (Exp 5.1 and 5.2) - and one of these experiments actually resulted in apparent pathogen avoidance inheritance in the F2 generation (but not in the F1). An alternative pathogen source was tested in only one biological replicate (Exp 3). Given the variability observed in the F2 generation, increasing biological replicates would have added to the strengths of the report.

We agree that our study was not exhaustive in our exploration of variables that might be interfering with our ability to detect F2 avoidance. We also note that some of these variables also failed (with many more independent experiments) to induce elevated daf-7p::gfp expression in ASI neurons in F2 progeny. Our goal was not to show that variation in some growth or assay condition would generate reproducible negative results, but the exploration was designed to tweak conditions to enable detection of a robust F2 response. Given the strength of the data presented in Moore et al., (2019) we expected that adjustment of the problematic variable would produce positive results apparent in a single replicate, which could then be followed up. If we had succeeded, then we would have documented the conditions that enabled robust F2 inheritance and would have explored molecular mechanisms that support this important but mysterious process.

(2) A key difference between the methods used here and those published previously, is an increase in the age of the animals used for training - from mostly L4 to mostly young adults. I was unable to find a clear example of an experiment when these two conditions were compared, although the authors state that it made no difference to their results.

We can state firmly that the apparent time delay did not affect P0 learned avoidance (new Figure S1) or, as documented in Table S1, daf-7p::gfp expression in ASI neurons. In our experience, training mostly L4’s on PA14 frequently failed to produce sufficient F1 embryos for both F1 avoidance assays or daf-7p::gfp measurements in ASI neurons and collection of F2 progeny. Indeed, in early attempts to detect heritable PA14 aversion, trained P0 and F1 progeny were not assayed in order to obtain sufficient F2’s for a choice assay. These animals failed to display aversion, but without evidence of successful P0 training or an F1 intergenerational response this was deemed a non-fruitful trouble-shooting approach. We have added supplemental Figure S1 which presents P0 choice assay results from experiments using younger trained animals that failed to produce sufficient F1’s to continue the inheritance experiments.

The different timing at the start of training between the two protocols may reflect the age of the recovered bleached P0 embryos. It is reasonable to assume that bleaching day 1 adults vs day 2 or 3 adults from the P-1 population could shift the average age of recovered P0 embryos by several hours. The Murphy protocol only states that P0 embryos were obtained by bleaching healthy adults. Regardless, if the hypothesis entertained here is true, that a several hour difference in larval/adult age during 24 hours of training affects F2 inheritance of learned aversion but does not affect P0 learned avoidance, then we would argue that this paradigm for heritable learned avoidance, as described in Moore et al., (2019, 2021), is not sufficiently robust for mechanistic investigations.

(3) The original paper reports a transgenerational avoidance effect up to the F5 generation. Although in this work the authors failed to see avoidance in the F2 generation, it would have been prudent to extend their tests for more generations in at least a couple of their experiments to ensure that the F2 generation was not an aberration (although this reviewer acknowledges that this seems unlikely to be the case).

We would point out that we also failed to robustly replicate the F2 response in the daf-7p::gfp expression assays. An F2-specific aberration that affects two different assays seems quite unlikely, and it remains unclear how we would interpret a positive result in F3 and F4 generations without a positive result in the F2 generation. Were we to further extend these investigations, we believe that exploration of additional culture conditions would warrant higher priority than extension of our results to the F3 and F4 generations.

Reviewing Editor Comments:

The reviewers' suggestions for improving the manuscript were mostly minor, to change the wording in some places and to add some more explanation regarding the methods.

What should be highlighted in the section on OP50 growth conditions is that the initial preference for PA14 in the Murphy lab has also been observed by multiple other labs (Bargmann, Kim, Zhang, Abbalay). The fact that this preference was not observed by the Hunter lab is one of several indicators of subtle differences in the environment that might add up to explain the differences in results.

We agree that subtle known and unknown differences in OP50 and PA14 culture conditions can have measurable effects on the detection of PA14 attraction/aversion relative to OP50 attraction/aversion that could obscure or create the appearance of heritable effects between generations. We have added (see below) to the text a fuller description of the variability in the initial or naive preference observed in different laboratories using similar or variant 2-choice assays and culture conditions. It is worth emphasizing that direct comparison of the OP50 growth conditions specified in Moore et al., (2021) frequently revealed a much larger effect on the naïve choice index than is reported between labs (Figure 4).  

“Naïve (OP50 grown) worms often show a bias towards PA14 in choice assays (Zhang et al., 2005; Ha et al., 2010; Moore et al., 2019; Pereira et al., 2020; Lalsiamthara and Aballay, 2022). This response, rather than representing an innate attraction to PA14, likely reflects the context of the worm's recent growth on OP50, a mild C. elegans pathogen (Garigan et al., 2002; Garsin et al., 2003; Shi et al., 2006). Thus, the naïve worms presented with a choice between a recently experienced mild pathogen (OP50) and a novel food choice (PA14) initially choose the novel food instead of the known mild pathogen (OP50 aversion).

In line with our results, some other groups have also reported higher naïve choice index scores (Lee et al., 2017). This variability in naïve choice may reflect differences in growth conditions of either the OP50 or PA14 bacteria. In addition, we note that among the studies that show naïve worm attraction to Pseudomonas (OP50 aversion) there are extensive methodological differences from the methods in Moore et al., (2019; 2021b), including differences in bacterial growth temperature, incubation time, whether the bacteria is diluted or concentrated prior to placement on the choice plates, the concentration of peptone in the choice plates, the length of the choice assay, and the inclusion of sodium azide in the choice assays (Zhang et al., 2005; Ha et al., 2010; Moore et al., 2019; Pereira et al 2020; Lalsiamthara and Aballay, 2022). Thus, the cause of the variability across published reports is not clear.”

Overall, an emphasis on the absence of robustness of the reported results, rather than failure to reproduce them (which can always have many reasons), is appropriate.

We agree that an emphasis on robustness is appropriate and have modified the text throughout the manuscript to shift the emphasis to absence of robustness. This includes a change to the manuscript title, which is now, “Reported transgenerational responses to Pseudomonas aeruginosa in C. elegans are not robust”

A significant experimental addition would be some attempts to determine whether the bacterial PA14 pathogen in the authors' lab produces the P11 small RNA, which has been proposed to have a causal role in initiating the previously reported transgenerational inheritance.

We acknowledge in the revised manuscript that a subsequent publication (Kaletsky et al., 2020) identified a correlation between PA14 training conditions that induced transgenerational memory and the expression of P11, a P. aeruginosa small non-coding RNA (see our response above to Reviewer #2’s similar query). While testing for the presence of P11 in Harvard culture conditions would be an important assay in any study whose purpose was to investigate the proposed P11-mediated mechanism underlying the transgenerational responses reported by the Murphy Lab, our goal was rather to replicate the robust transgenerational (F2) responses to PA14 training and then to investigate in more detail how sid-1 and sid-2 contribute to transgenerational epigenetic inheritance. Neither sid-1 nor sid-2 are predicted to transport small RNAs or single-stranded RNAs, thus testing for the presence of P11 is less relevant to our goals. Regardless, we note that Figure 3L in Kaletsky et al., (2020) showed that PA14 ΔP11 bacteria failed to induce an F1 avoidance response. Thus, the fact that we observed F1 avoidance implies that our culture conditions successfully induced P11 expression.

Reviewer #1 (Recommendations For The Authors):

The abstract could be more positive by concluding that 'We conclude that this example of transgenerational inheritance lacks robustness but instead reflects an example of small RNA-mediated intergenerational inheritance.'

As recommended, we have added additional clarifying information to the abstract and moderated the conclusion sentence.

“We did confirm that the dsRNA transport proteins SID-1 and SID-2 are required for the intergenerational (F1) inheritance of pathogen avoidance, but not for the F1 inheritance of elevated daf-7 expression. Furthermore, our reanalysis of RNA seq data provides additional evidence that this intergenerational inherited PA14 response may be mediated by small RNAs.”

“We conclude that this example of transgenerational inheritance lacks robustness, confirm that the intergenerational avoidance response, but not the elevated daf-7p::gfp expression in F1 progeny, requires sid-1 and sid-2, and identify candidate siRNAs and target genes that may mediate this intergenerational response.”

Differential expression of sRNAs or mRNAs might be better understood quantitatively by presenting data in scatterplots (Reed and Montgomery 2020) rather than in volcano plots.

We agree and have modified Figure 6A and 6B.

This statement in the main text might be unnecessary, as it affects the tenor of the conclusion of this significant manuscript. 'We note that none of the raw data for the published figures and unpublished replicate experiments . . . this hampered our ability to fully compare'.

We have rewritten this paragraph to focus on our goal: to identify the source of the discrepancy between our results and the published results. We considered discarding this statement but ultimately decided that our inability to directly compare our data to that of previously published work is a shortcoming of our study that deserves to be acknowledged and explained.

“Ideally, we would have compared our results with the published results (Moore et al., 2019), to possibly identify additional experimental parameters for further investigation; for example, a quantitative comparison of naïve choice in the P0 and F1 generations could help to determine the role of bacterial growth in the choice assay response. However, none of the raw data for the published figures and unpublished replicate experiments (Moore et al., 2019) were available on the publisher’s website or provided upon request to the corresponding author. In the absence of a quantitative comparison, it remains possible that an explanation for the discrepancies between our results and those of Moore et al., (2019) has been overlooked.”

The final sentence of the Discussion could be tempered and more positive by stating 'Thus independent reproducibility is of paramount concern, and we have tried to be completely transparent as a model for how heritability research should be conducted within the C. elegans community'.

Thank you. The suggested sentence nicely captures our intention. We now use it, almost verbatim, as our final sentence.

“Thus, independent reproducibility is of paramount concern, and we have tried to be completely transparent as a model for how heritability research should be presented within the C. elegans community.”

Reviewer #2 (Recommendations For The Authors):

Specific comments:

(1) Protocol: It is difficult to assess from the Methods the exact protocol used by the authors to assay food preference. The annotated Murphy protocol is not sufficient. The authors should provide their own protocol - a detailed lab-ready protocol where every step is outlined, and any steps that deviate from the Murphy lab protocol are called out.

Thank you for this excellent suggestion. We now include a protocol that documents the precise steps, timings, and controls that we followed (S1_aversion_protocol). We also include footnotes to both explain the reasons behind particular steps and to document known differences to the published protocol. Given the thoroughness of this suggested approach, we have thus removed the annotated version of Moore et al., (2021) from the revised submission.

(2) The authors imply in the methods that, unlike the Murphy lab, they did NOT use azide in the assay, and instead used 4oC to "freeze" the worms in place - It is not clear whether this method was used throughout all their assays and whether this could be a source of the difference. This change is NOT indicated in the annotated Murphy lab STAR Protocol they provide in the supplement.

We apologize for the lack of clarity. Concerned that azide may be interfering with our ability to detect heritable silencing we tested and then used cold-induced rigor to preserve worm choice in some choice assay results. This was not a change to the core protocol, but a variation used in some assays to determine whether azide could reduce our ability to detect heritable behavioral responses to PA14 exposure. As Moore et al., (2021) show, too much azide can affect measurement of worm choice. Too little or ineffective azide also can affect measurement of worm choice. Azide also affects bacteria (both OP50 and PA14), which could affect the production of molecules that attract or repel worms, much like performing the assay in light vs dark conditions can influence the measured choice index.

In our hands, cold-induced rigor worked well and within biological replicates was indistinguishable from azide (Figure S10). Thus, we include those results in our analysis and now indicate in Tables 2 and S2 and in Figures 1 and 3 which experiments used which method. As suggested, we now provide a detailed protocol that includes a note describing our precise method for cold-induced rigor.

Also, the number of worms used in each assay needs to be specified (same or different from Murphy protocol?), and whether any worms were "censored" as in the Murphy protocol, and if so on what basis.

While we published the exact number of worms scored in each assay (on each plate) it is unknown how this might compare to the results published in Moore et al., (2019), as the number of animals in the presented choice assays (either per plate or per choice) were not reported. Details on censoring, when to exclude data, and additional criteria to abandon an in-progress experiment are now detailed in the protocol (S1_aversion_protocol)

(3) Several instances in the text cite changes in the protocol as producing "no meaningful differences" without referring to a specific experiment that supports that statement (for example, line 399 regarding azide).

We now include data and methods comparing azide and cold-induced rigor (Supplemental document S1_aversion_protocol, Supplemental Figure S10), and data showing the P0 choice index for 48-52 hour post-bleach L4/young adults (Supplemental Figure S1), in addition to the previously noted absence of effects due to differences in embryo bleaching protocols (Figures 2, 3 and Tables 1, 2, S1, and S2).

(4) If the authors want to claim the irreproducibility of the Murphy lab results, they should use the exact protocol used by the Murphy lab in its entirety. It is not sufficient to show that individual changes do not affect the outcome, since the protocol they use appears to include SEVERAL changes which could cumulatively affect the results. If the authors do not want to do this, they should at least acknowledge and summarize in their discussion ALL their protocol changes.

We acknowledge these minor differences between the protocols we followed and the published methods but disagree that they invalidate our results. We transparently present the effect of known minimal protocol changes. We also present analysis of possible invalidating variations (number of animals in a choice assay). We emphasize that in our hands both measures of TEI, the choice assay and measurement of daf-7p::gfp in ASI neurons, failed to replicate the published transgenerational results.

If the protocol is sensitive to how animals are counted, whether bleached embryos are mixed gently or vigorously or a few hours difference in age at training, then in our view this TEI paradigm is not robust.

See also our response to reviewer #3’s public reviews above.

(5) The authors acknowledge that "non-obvious growth culture differences" could account for the different results. In this respect, the Murphy lab has proposed that the transgenerational effect requires a small RNA expressed in PA14. The authors should check that this RNA is expressed in the cultures they grow in their lab and use for their experiments. This could potentially identify where the two protocols diverge.

The bacterial culture conditions and worm training procedures described in Moore et al., (2019) successfully produced trained P0 animals that transmitted a PA14 aversion response to their F1 progeny. In a subsequent publication (Kaletsky et al., 2020), the Murphy lab showed a correlation between the culture conditions that induce heritable avoidance and the expression of P11, a P. aeruginosa small non-coding RNA. As mentioned above in response to Reviewer #2’s public review and the Reviewing Editor’s comments to authors, the Murphy lab showed that PA14 ΔP11 bacteria fail to induce an F1 avoidance response (Figure 3L in Kaletsky et al., (2020)). Thus, the fact that we observed F1 avoidance implies that our culture conditions successfully induced P11 expression. We believe that this addresses the concern raised here. Furthermore, if P11 is not reliably expressed in pathogenic PA14, then the published model is unlikely to be relevant in a natural environment. Again, we thank the reviewer for raising this issue and have added this information to the revised manuscript (see above response to Reviewer #2’s Public Reviews).

(6) Legend to Figure 1: please clarify which experiments were done with which PA14 isolates especially for A-C. What is the origin of the N2 strain used here?

These details from Tables 2 and S2 have been added to Figure 1 panels A-C and Figure 3. Bristol N2, obtained from the CGC (reference 257), was used for aversion experiments.

(7) Growth conditions: "These young adults produced comparable P0 and F1 results (Figure 1, Figure 2, and Figure 3)." It is not clear from the text what specific figure panels need to be compared to examine the effect of the variables described in the text. Please indicate which figure panels should be compared (lines 70-95).

The information for the daf-7p::gfp expression experiments displayed in Figure 1 and Figure 2 is presented in Table 1 and Table S1. The data for P0 aversion training using younger animals is now presented in Figure S1.

Reviewer #3 (Recommendations For The Authors):

While overall I found this easy to follow and well-written, I think the clarity of the figures could be improved by incorporating some of the information from S2 into Figure 3. Besides the figure label listing the experiment (Exp1, Exp2, etc) it would be helpful to add pertinent information about the experiment. For example Exp 1.1 (light, 20{degree sign}C), Exp1.2 (dark, 20{degree sign}C), Exp 5 (25{degree sign}C, light), etc.

Thank you for the suggestion. These details from Tables 2 and S2 have been added to Figures 1 A-C, and 3.

Citations

• Moore, R.S., Kaletsky, R., and Murphy, C.T. (2019). Piwi/PRG-1 Argonaute and TGF-beta Mediate Transgenerational Learned Pathogenic Avoidance. Cell 177, 1827-1841 e1812.

• Moore, R.S., Kaletsky, R., and Murphy, C.T. (2021). Protocol for transgenerational learned pathogen avoidance behavior assays in Caenorhabditis elegans. STAR Protoc 2, 100384.

• Kaletsky, R., Moore, R.S., Vrla, G.D., Parsons, L.R., Gitai, Z., and Murphy, C.T. (2020). C. elegans interprets bacterial non-coding RNAs to learn pathogenic avoidance. Nature 586, 445-451.

• Pereira, A.G., Gracida, X., Kagias, K., and Zhang, Y. (2020). C. elegans aversive olfactory learning generates diverse intergenerational effects. J Neurogenet 34, 378-388.

eLife Assessment

This work investigates ZC3H11A as a cause of high myopia through the analysis of human data and experiments with genetic knockout of Zc3h11a in mouse, providing a useful model of myopia. The evidence supporting the conclusion is still incomplete in the revised manuscript as the concerns raised in the previous review were not fully addressed. The article will benefit from further strengthening the genetic analysis, full presentation of human phenotypic data, and explaining the reasons why there was no increased axial length in mice with myopia. The work will be of interest to ophthalmologists and researchers working on myopia.

Reviewer #2 (Public review):

Summary:

The authors reported that mutations were identified in the ZC3H11A gene in four adolescents from 1015 high myopia subjects in their myopia cohort. They further generated Zc3h11a knockout mice utilizing the CRISPR/Cas9 technology.

Comments on revisions:

Chong Chen and colleagues revised the manuscript; however, none of my suggestions from the initial review have been sufficiently addressed.

(1) I indicated that the pathogenicity and novelty of the mutation need to be determined according to established guidelines and databases. However, the conclusion was still drawn without sufficient justification.<br /> (2) The phenotype of heterozygous mutant mice is too weak to support the gene's contribution to high myopia. The revised manuscript does not adequately address these discrepancies. Furthermore, no explanation was provided for why conditional gene deletion was not used to avoid embryonic lethality, nor was there any discussion on tissue- or cell-specific mechanistic investigations.<br /> (3) The title, abstract, and main text continue to misrepresent the role of the inflammatory intracellular PI3K-AKT and NF-κB signaling cascade in inducing high myopia. No specific cell types have been identified as contributors to the phenotype. The mice did not develop high myopia, and no relationship between intracellular signaling and myopia progression has been demonstrated in this study.

Reviewer #3 (Public review):

Chen et al have identified a new candidate gene for high myopia, ZC3H11A, and using a knock-out mouse model, have attempted to validate it as a myopia gene and explain a potential mechanism. They identified 4 heterozygous missense variants in highly myopic teenagers. These variants are in conserved regions of the protein, and predicted to be damaging, but the only evidence the authors provide that these specific variants affect protein function is a supplement figure showing decreased levels of IκBα after transfection with overexpression plasmids (not specified what type of cells were transfected). This does not prove that these mutations cause loss of function, in fact it implies they have a gain-of-function mechanism. They then created a knock-out mouse. Heterozygotes show myopia at all ages examined but increased axial length only at very early ages. Unfortunately, the authors do not address this point or examine corneal structure in these animals. They show that the mice have decreased B-wave amplitude on electroretinogram (a sign of retinal dysfunction associated with bipolar cells), and decreased expression of a bipolar cell marker, PKCα. On electron microscopy, there are morphologic differences in the outer nuclear layer (where bipolar, amacrine, and horizontal cell bodies reside). Transcriptome analysis identified over 700 differentially expressed genes. The authors chose to focus on the PI3K-AKT and NF-κB signaling pathways and show changes in expression of genes and proteins in those pathways, including PI3K, AKT, IκBα, NF-κB, TGF-β1, MMP-2 and IL-6, although there is very high variability between animals. They propose that myopia may develop in these animals either as a result of visual abnormality (decreased bipolar cell function in the retina) or by alteration of NF-κB signaling. These data provide an interesting new candidate variant for development of high myopia, and provide additional data that MMP2 and IL6 have a role in myopia development. For this revision, none of my previous suggestions have been addressed.

Author response:

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

Reviewer #1 (Public Review):

Chen and colleagues investigated ZC3H11A as a potential cause of high myopia (HM) in humans through the analysis of exome sequencing in 1,015 adolescents and experiments involving Zc3h11a knock-out mice. The authors showed four possibly pathogenic missense variants in four adolescents with HM. After that, the authors presented the phenotypic features of Zc3h11a knock-out mice, the result of RNA-sequencing, and a comparison of mRNA and protein levels of the functional candidates between wild-type and Zc3h11a knock-out mice. Based on their observations, the authors concluded that ZC3H11A protein contributes to the early onset of myopia.

The strengths of this manuscript include: (1) successful identification of characteristic ophthalmic phenotypes in Zc3h11a knock-out mice, (2) demonstration of biological features related to myopia, such as PI3K-AKT and NF-kB pathways, and (3) inclusion of supporting human genetic data in individuals with HM. On the other hand, the weaknesses of this paper appear to be: (1) the lack of robust evidence from their genomic analysis, and (2) insufficient evidence to support phenotypic similarity between humans with ZC3H11A mutations and Zc3h11a knock-out mice. Given that the biological mechanisms of high myopia are not fully understood, the identification of a novel gene is valuable. As described in the manuscript, it is worth noting that the previous study using myopic mouse model has implicated the role of ZC3H11A in the etiology of myopia (Fan et al. Plos Genet 2012).

Thank you very much for your valuable suggestions.

Specific comments:

(1) I am concerned about the certainty of similarity in phenotypes between individuals with ZC3H11A mutation and Zc3h11a knock-out mice. A crucial point would be that there are no statistical differences in axial lengths (ALs) between wild-type and Zc3h11a knock-out mice at 8W and 10W, even though ALs in the individuals with ZC3H11A mutation were long. I would also like to note that the phenotypic information of these individuals is not available in the manuscript, although the authors indicated the suppressed b-wave amplitude in Zc3h11a knock-out mice. Considering that the authors described that "Detailed ophthalmic examinations were performed (lines: 321-323)", the detailed clinical features of these individuals should be included in the manuscript.

Thank you for your valuable comments. The axial length in Zc3h11a Het-KO mice were found to be significantly greater than in WT littermates at weeks 4 and 6 (Independent samples t-test, p<0.05; Figure 2A and B). Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

Additionally, regarding the “detailed ophthalmic examinations”, due to our patients were selected from a myopia screening cohort of over one million (children and adolescents myopia survey [CAMS] program), and ophthalmic examination only includes semi-annual refractive error measurements (a total of 5 times, with refractive error being the average of the three maximum values) and only one axial length measurement. The inappropriate description of “Detailed clinical features” has been removed.

(2) The term "pathogenic variant" should be used cautiously. Please clarify the pathogenicity of the reported variants in accordance with the ACMG guideline.

Thank you for your valuable comments. Four missense mutations in the ZC3H11A gene (c.412G>A, p.V138I; c.128G>A, p.G43E; c.461C>T, p.P154L; and c.2239T>A, p.S747T) were identified in the 1015 HM patients aged from 15 to 18 years. All of the identified mutations exhibited very low frequencies or does not exist in the Genome Aggregation Database (gnomAD) and Clinvar, and using pathogenicity prediction software SIFT, PolyPhen2, and CADD, most of them display high pathogenicity levels. Among them, c.412G>A, c.128G>A and c.461C>T were located in or around a domain named zf-CCCH_3 (Figure 1A and B). Furthermore, all of the mutation sites were located in highly conserved amino acids across different species (Figure 1C). Four mutations resulted in a higher degree of conformational flexibility and altered the negative charge at the corresponding sites (Figure 1D and E). Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3). According to the ACMG guidelines, the above mutations can be classified as “Pathogenic Moderate”.

(3) The genetic analysis does not fully support the claim that ZC3H11A is causative for HM. While the authors showed the rare allele frequencies and high CADD scores (> 20) of the identified variants, these were insufficient to establish causality. A helpful way to assess the causality would be performing a segregation analysis. An alternative approach is to show significant association by performing a gene-level association test. Assessing the pathogenicity of the variants using various prediction software, such as SIFT, PolyPhen2, and REVEL may also provide additional supportive evidence.

Thank you for your valuable comments. We have addad the pathogenicity of the variants using various prediction software, such as SIFT, PolyPhen2, CADD, and the population variation databases, such as Genome Aggregation Database (gnomAD_AF) and ClinVar. Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3).

(4) As shown in Figure 2, significant differences in refraction were observed from 4 weeks to 10 weeks. Nevertheless, no differences were observed in AL, anterior/vitreous chamber depth, and lens depth. The author should experimentally clarify what factors contribute to the observed difference in refraction.

Thank you for your valuable comments. The existing data show significant differences in refraction between 4 and 10 weeks, with the AL and vitreous cavity depth of Het mice being longer than those of WT mice at 4 and 6 weeks. Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

(5) The gene names should be italicized throughout the manuscript.

Thank you for your valuable comments. The gene names have been italicized throughout the manuscript.

(6) Table 1: providing chromosomal positions and rs numbers (if available) would be helpful for readers.

Thank you for your valuable comments. We have provided the chromosome positions and rs number (if available) of each mutation in Table 1.

(7) Figure 5b, c, and d: the results of pathway analysis and GO enrichment analysis are difficult to interpret due to the small font size. It would be preferable to present these results in tables. Moreover, the authors should set a significant threshold in the enrichment analyses.

Thank you for your valuable comments. We have adjusted the font size of the image. In the retina transcriptome analysis, we have set Fold change (FC) of at least two and a P value < 0.05 as thresholds to analyze differentially expressed genes (DEGs). The GO terms and KEGG pathways enrichment analysis selected the top 20 with the most significant differences or the highest number of enriched genes for display.

Reviewer #2 (Public Review):

Summary: Chong Chen and colleagues reported that mutations were identified in the ZC3H11A gene in four adolescents from 1015 high myopia subjects in their myopia cohort. They further generated Zc3h11a knockout mice utilizing the CRISPR/Cas9 technology. They analyzed the heterozygotes knockout mice compared to control littermates and found refractive error changes, electrophysiological differences, and retinal inflammation-related gene expression differences. They concluded that ZC3H11A may play a role in the early onset of myopia by regulating inflammatory responses.

Strengths:

Data were shown from both clinical cohort and animal models.

Weaknesses:

Their findings are interesting and important, however; they need to resolve several points to make the current conclusion.

(1) They described the ZC3H11A gene as a pathogenic variant for high myopia. It should be classified as pathogenic according to the guidelines of the American College of Medical Genetics and Genomics (Richards et al., Genet Med 17(5):405-24, 2015). The modes of inheritance for the families need to be shown. They also described identifying the gene as a "new" candidate. It should be checked in databases such as gnomAD and ClinVar, and any previous publications and be declared as a novel variant.

Thank you for your valuable comments. Four missense mutations in the ZC3H11A gene (c.412G>A, p.V138I; c.128G>A, p.G43E; c.461C>T, p.P154L; and c.2239T>A, p.S747T) were identified in the 1015 HM patients aged from 15 to 18 years. All of the identified mutations exhibited very low frequencies or does not exist in the Genome Aggregation Database (gnomAD) and Clinvar, and using pathogenicity prediction software SIFT, PolyPhen2, and CADD, most of them display high pathogenicity levels. Among them, c.412G>A, c.128G>A and c.461C>T were located in or around a domain named zf-CCCH_3 (Figure 1A and B). Furthermore, all of the mutation sites were located in highly conserved amino acids across different species (Figure 1C). Four mutations resulted in a higher degree of conformational flexibility and altered the negative charge at the corresponding sites (Figure 1D and E). Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3). According to the ACMG guidelines, the above mutations can be classified as “Pathogenic Moderate”.

Unfortunately, our patients are part of the MAGIC project (aged 15 years or older), a cohort consists of thousands of individuals with HM (patients from the children and adolescents myopia survey [CAMS] program) who have undergone WES, and their parents' relevant information was not collected for performing a segregation analysis.

(2) The phenotypes of the heterozygote mice are weak overall. The het mice showed mild to moderate myopic refractive shifts from 4 to 10 weeks of age. However, this cannot be explained by other ocular biometrics such as anterior chamber depth or lens thickness. Some differences are found between het and WT littermates in axial length and vitreous chamber depth but disappear after 8 weeks old. Furthermore, the early differences are not enough to explain the refractive error changes. They mentioned that they did not use homozygotes because of the embryonic lethality. I would strongly suggest employing conditional knockout systems to analyze homozygotes. This will also be able to identify the causative tissues/cells because they assume bipolar cells are functional. The cells in the retinal pigment epithelium and choroid are also important to contribute to myopia development.

Thank you for your valuable comments. The existing data show significant differences in refraction between 4 and 10 weeks, with the AL and vitreous cavity depth of Het mice being longer than those of WT mice at 4 and 6 weeks. Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

The drawback is that, we did not conduct relevant research on homozygous knockout mice. The first reason is that our patient's mutation pattern is heterozygous mutation (Heterozygous knockout mice can better simulate human phenotypes). The second reason is that homozygous knockout mice are lethal, and we did not use the conditional knockout mouse model for further research. At the same time, we limited the pathway of myopia to the recognized and classical retina-sclera pathway, and did not study other pathways such as retinal pigment epithelium and choroid.

(3) Their hypothesis regarding inflammatory gene changes and myopic development is not logical. Are the inflammatory responses evoked from bipolar cells? Did the mice show an accumulation of inflammatory cells in the inner retina? Visible retinal inflammation is not generally seen in either early-onset or high-myopia human subjects. Can this be seen in the actual subjects in the cohort? To me, this is difficult to adapt the retina-to-sclera signaling they mentioned in the discussion so far. Egr-1 may be examined as described.

Thank you for your valuable comments. We have removed the hypothesis regarding inflammatory gene changes and myopic development. At present, the explanation is based solely on the correlation of signal pathways, the theoretical basis comes from the reference literature:

“Lin et al., Role of Chronic Inflammation in Myopia Progression: Clinical Evidence and Experimental Validation. EBioMedicine, 2016 Aug:10:269-81, Figure 7.”

Reviewer #3 (Public Review):

Chen et al have identified a new candidate gene for high myopia, ZC3H11A, and using a knock-out mouse model, have attempted to validate it as a myopia gene and explain a potential mechanism. They identified 4 heterozygous missense variants in highly myopic teenagers. These variants are in conserved regions of the protein, but the authors provide no evidence that these specific variants affect protein function. They then created a knock-out mouse. Heterozygotes show myopia at all ages examined but increased axial length only at very early ages. Unfortunately, the authors do not address this point or examine corneal structure in these animals. They show that the mice have decreased B-wave amplitude on electroretinogram (a sign of retinal dysfunction associated with bipolar cells), and decreased expression of a bipolar cell marker, PKCa. They do not address, however, whether there are fewer bipolar cells, or simply decreased expression of the marker protein. On electron microscopy, there are morphologic differences in the outer nuclear layer (where bipolar, amacrine, and horizontal cell bodies reside). Transcriptome analysis identified over 700 differentially expressed genes. The authors chose to focus on the PI3K-AKT and NF-kB signaling pathways and show changes in the expression of genes and proteins in those pathways, including PI3K, AKT, IkBa, NF-kB, TGF-b1, MMP-2, and IL-6, although there is very high variability between animals. They propose that myopia may develop in these animals either as a result of visual abnormality (decreased bipolar cell function in the retina) or by alteration of NF-kB signaling. These data provide an interesting new candidate variant for the development of high myopia, and provide additional data that MMP2 and IL6 have a role in myopia development, but do not support the claim of the title that myopia is caused by an inflammatory reaction.

Thank you for your valuable comments. Four missense mutations in the ZC3H11A gene (c.412G>A, p.V138I; c.128G>A, p.G43E; c.461C>T, p.P154L; and c.2239T>A, p.S747T) were identified in the 1015 HM patients aged from 15 to 18 years. All of the identified mutations exhibited very low frequencies or does not exist in the Genome Aggregation Database (gnomAD) and Clinvar, and using pathogenicity prediction software SIFT, PolyPhen2, and CADD, most of them display high pathogenicity levels. Among them, c.412G>A, c.128G>A and c.461C>T were located in or around a domain named zf-CCCH_3 (Figure 1A and B). Furthermore, all of the mutation sites were located in highly conserved amino acids across different species (Figure 1C). Four mutations resulted in a higher degree of conformational flexibility and altered the negative charge at the corresponding sites (Figure 1D and E). Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3). According to the ACMG guidelines, the above mutations can be classified as “Pathogenic Moderate”.

The existing data show significant differences in refraction between 4 and 10 weeks, with the AL and vitreous cavity depth of Het mice being longer than those of WT mice at 4 and 6 weeks. Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

To evaluate the change in the number of a specific type of retinal cells, the most commonly used experimental method involves staining with antibodies specific to the target cell type, followed by fluorescence microscopy. The fluorescence intensity or the number of cells can be analyzed semi-quantitatively to assess the changes in the specific cell type in the retina. For example, in retinal degenerative models, rhodopsin-specific staining is used to identify the loss of rod cells. In our study, we selected PCK-α as a marker protein for bipolar cells to assess their number. Additionally, transmission electron microscopy (TEM) was used to observe damage to the cell morphology in the inner nuclear layer (INL) of Het mice, where bipolar cell bodies are located. Based on both sets of data, we conclude that bipolar cells have indeed undergone structural damage and a reduction in number.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

We have removed the hypothesis regarding inflammatory gene changes and myopic development. At present, the explanation is based solely on the correlation of signal pathways, the theoretical basis comes from the reference literature:

“Lin et al., Role of Chronic Inflammation in Myopia Progression: Clinical Evidence and Experimental Validation. EBioMedicine, 2016 Aug:10:269-81, Figure 7.”

eLife Assessment

This study follows up on Arimura et al's powerful new method MagIC-Cryo-EM for imaging native complexes at high resolution. Using a clever design embedding protein spacers between the antibody and the nucleosomes purified, thereby minimizing interference from the beads, the authors concentrate linker histone variant H1.8 containing nucleosomes. From these samples, the authors obtain convincing atomic structures of the H1.8 bound chromatosome purified from interphase and metaphase cells, finding a NPM2 chaperone bound form exists as well. Caveats previously noted have been addressed nicely in the revision, strengthening the overall conclusions. This is an important new tool in the arsenal of single molecule biologists, permitting a deep dive into structure of native complexes, and will be of high interest to a broad swathe of scientists studying native macromolecules present at low concentrations in cells.

Reviewer #1 (Public review):

Summary:

In this manuscript, Arimura et al describe MagIC-Cryo-EM, an innovative method for immune-selective concentrating of native molecules and macromolecular complexes for Cryo-EM imaging and single-particle analysis. Typically, Cryo-EM imaging requires much larger concentrations of biomolecules than those that are feasible to achieve by conventional biochemical fractionation. This manuscript is meticulously and clearly written and the new technique is likely to become a great asset to other electron microscopists and chromatin researchers.

Strengths:

Previously, Arimura et al. (Mol. Cell 2021) isolated from Xenopus extract and resolved by Cryo-EM a sub-class of native nucleosomes conjugated containing histone H1.8 at the on-dyad position, similar to that previously observed by other researchers with reconstituted nucleosomes. Here they sought to analyze immuno-selected nucleosomes aiming to observe specific modes of H1.8 positioning (e.g. on-dyad and off-dyad) and potentially reveal structural motifs responsible for the decreased affinity of H1.8 for the interphase chromatin compared to metaphase chromosomes. The main strength of this work is a clever and novel methodological design, in particular the engineered protein spacers to separate captured nucleosomes from streptavidin beads for clear imaging. The authors provide a detailed step-by-step description of MagIC-Cryo-EM procedure including nucleosome isolation, preparation of GFP nanobody attached magnetic beads, optimization of the spacer length, concentration of the nucleosomes on graphene grids, data collection and analysis, including their new DUSTER method to filter-out low signal particles. This tour de force methodology should facilitate the consideration of MagIC-Cryo-EM by other electron microscopists, especially for analysis of native nucleosome complexes.<br /> In pursuit of biologically important new structures, the immune-selected H1.8-containing nucleosomes were solved at about 4A resolution; their structure appears to be very similar to the previously determined structure of H1.8-reconstituted nucleosomes. There were no apparent differences between the metaphase and interphase complexes suggesting that the on-dyad and off-dyad positioning does not explain the differences in H1.8 - nucleosome binding. However, they were able to identify and solve complexes of H1.8-GFP with histone chaperone NPM2 in a closed and open conformation providing mechanistic insights for H1-NPM2 binding and the reduced affinity of H1.8 to interphase chromatin as compared to metaphase chromosomes.

MagIC technique still has certain limitations resulting from formaldehyde fixation, use of bacterial-expressed recombinant H1.8-GFP, and potential effects of magnetic beads and/or spacer on protein structure, which are explicitly discussed in the text. Notwithstanding these limitations, MagIC-Cryo-EM is expected to become a great asset to other electron microscopists and biochemists studying native macromolecular complexes.

Comments on revisions:

In the revision, Arimura et al. have constructively addressed the reviewer's concerns, by discussing possible limitations and including additional information on proteomic analysis and H1.8-NPM2 structures.<br /> The revised manuscript and rebuttal letter strengthen my initial opinion that this paper describes an innovative method for immune-selective concentrating of native molecules and macromolecular complexes thus enabling Cryo-EM imaging and structural analysis of native nucleosome complexes at low concentration. This manuscript is meticulously and clearly written and may become a great asset to other electron microscopists and chromatin researchers

Reviewer #2 (Public review):

Summary:

The authors present a straightforward and convincing demonstration of a reagent and workflow that they collectively term "MagIC-cryo-EM", in which magnetic nanobeads combined with affinity linkers are used to specifically immobilize and locally concentrate complexes that contain a protein-of-interest. As a proof of concept, they localize, image, and reconstruct H1.8-bound nucleosomes reconstructed from frog egg extracts. The authors additionally devised an image-processing workflow termed "DuSTER", which increases the true positive detections of the partially ordered NPM2 complex. The analysis of the NPM2 complex {plus minus} H1.8 was challenging because only ~60 kDa of protein mass was ordered. Overall, single-particle cryo-EM practitioners should find this study useful.

Strengths:

The rationale is very logical and the data are convincing.

Weaknesses:

I have seen an earlier version of this study at a conference. The conference presentation was much easier to follow than the current manuscript. It is as if this manuscript had undergone review at another journal and includes additional experiments to satisfy previous reviewers. Specifically, the NPM2 results don't seem to add much to the main story (MagIC-cryo-EM) and read more like an addendum. The authors could probably publish the NPM2 results separately, which would make the core MagIC results (sans DusTER) easier to read.

Comments on revisions:

The authors have addressed my concerns. Congratulations!

Author response:

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

Reviewer #1 (Public review):

Summary:

In this manuscript, Arimura et al describe MagIC-Cryo-EM, an innovative method for immune-selective concentrating of native molecules and macromolecular complexes for Cryo-EM imaging and single-particle analysis. Typically, Cryo-EM imaging requires much larger concentrations of biomolecules than that are feasible to achieve by conventional biochemical fractionation. Overall, this manuscript is meticulously and clearly written and may become a great asset to other electron microscopists and chromatin researchers.

Strengths:

Previously, Arimura et al. (Mol. Cell 2021) isolated from Xenopus extract and resolved by Cryo-EM a sub-class of native nucleosomes conjugated containing histone H1.8 at the on-dyad position, similar to that previously observed by other researchers with reconstituted nucleosomes. Here they sought to analyze immuno-selected nucleosomes aiming to observe specific modes of H1.8 positioning (e.g. on-dyad and off-dyad) and potentially reveal structural motifs responsible for the decreased affinity of H1.8 for the interphase chromatin compared to metaphase chromosomes. The main strength of this work is a clever and novel methodological design, in particular the engineered protein spacers to separate captured nucleosomes from streptavidin beads for a clear imaging. The authors provide a detailed step-by-step description of MagIC-Cryo-EM procedure including nucleosome isolation, preparation of GFP nanobody attached magnetic beads, optimization of the spacer length, concentration of the nucleosomes on graphene grids, data collection and analysis, including their new DUSTER method to filter-out low signal particles. This tour de force methodology should facilitate considering of MagIC-CryoEM by other electron microscopists especially for analysis of native nucleosome complexes.

In pursue of biologically important new structures, the immune-selected H1.8-containing nucleosomes were solved at about 4A resolution; their structure appears to be very similar to the previously determined structure of H1.8-reconstituted nucleosomes. There were no apparent differences between the metaphase and interphase complexes suggesting that the on-dyad and off-dyad positioning does not explain the differences in H1.8 - nucleosome binding. However, they were able to identify and solve complexes of H1.8-GFP with histone chaperone NPM2 in a closed and open conformation providing mechanistic insights for H1-NPM2 binding and the reduced affinity of H1.8 to interphase chromatin as compared to metaphase chromosomes.

Weaknesses:

Still, I feel that there are certain limitations and potential artifacts resulting from formaldehyde fixation, use of bacterial-expressed recombinant H1.8-GFP, and potential effects of magnetic beads and/or spacer on protein structure, that should be more explicitly discussed. 

We thank the reviewer for recognizing the significance of our methods and for constructive comments. To respond to the reviewer's criticism, we revised the “Limitation of the study” section (page 12, line 420) as indicated by the underlines below.

“While MagIC-cryo-EM is envisioned as a versatile approach suitable for various biomolecules from diverse sources, including cultured cells and tissues, it has thus far been tested only with H1.8-bound nucleosome and H1.8-bound NPM2, both using antiGFP nanobodies to isolate GFP-tagged H1.8 from chromosomes assembled in Xenopus egg extracts after pre-fractionation of chromatin. To apply MagIC-cryo-EM for the other targets, the following factors must be considered: 1) Pre-fractionation. This step (e.g., density gradient or gel filtration) may be necessary to enrich the target protein in a specific complex from other diverse forms (such as monomeric forms, subcomplexes, and protein aggregates). 2) Avoiding bead aggregation. Beads may be clustered by targets (if the target complex contains multiple affinity tags or is aggregated), nonspecific binders, and the target capture modules. To directly apply antibodies that recognize the native targets and specific modifications, optimization to avoid bead aggregation will be important. 3) Stabilizing complexes. The target complexes must be stable during the sample preparation. Crosslink was necessary for the H1.8-GFP-bound nucleosome. 4) Loading the optimum number of targets on the bead. The optimal number of particles per bead differs depending on target sizes, as larger targets are more likely to overlap. For H1.8-GFP-bound nucleosomes, 500 to 2,000 particles per bead were optimal. We expect that fewer particles should be coated for larger targets.”

We would like to note that while the use of bacterially expressed GFP-tagged H1.8 and MagIC-cryo-EM may potentially influence the structure of the H1.8-bound nucleosome, the structures of GFP-tagged H1.8-bound nucleosomes isolated from chromosomes assembled in Xenopus egg extract are essentially identical to the endogenous H1.8bound nucleosome structure we previously determined. In addition, we have shown that GFP-H1.8 was able to replace the function of endogenous H1.8 to support the proper mitotic chromosome length (Fig. S3), which is based on the capacity of H1.8 to compete with condensin as we have previously demonstrated (PMID 34406118). Therefore, we believe that the effects of GFP-tagging to be minimal. This point incorporated into the main result section (page 6, line 215) to read as “The structures of GFP-tagged H1.8bound nucleosomes isolated from Xenopus egg extract chromosomes are essentially identical to the endogenous H1.8-bound nucleosome structure we previously determined. Therefore, although the usage of GFP-tagged H1.8 and MagIC-cryo-EM potentially influence the structure of the H1.8-bound nucleosome, we consider these influences to be minimal.”

Also, the GFP-pulled down H1.8 nucleosomes should be better characterized biochemically to determine the actual linker DNA lengths (which are known to have a strong effect of linker histone affinity) and presence or absence of other factors such as HMG proteins that may compete with linker histones and cause the multiplicity of nucleosome structural classes (such as shown on Fig. 3F) for which the association with H1.8 is uncertain.

We addressed the concerns brought by the reviewer as following:

(1) DNA length

As the reviewer correctly pointed out, linker DNA length is critical for linker histone binding, and conventional ChIP protocols often result in DNA over-digestion to lengths of 140–150 bp. To minimize DNA over-digestion and structural damage, we have optimized a gentle chromosomal nucleosome purification protocol that enabled the cryoEM analysis of chromosomal nucleosomes (PMID: 34478647). This protocol involves DNA digestion with a minimal amount of MNase at 4ºC, producing nucleosomal DNA fragments of 180–200 bp. Additionally, before each chromatin extraction, we performed small-scale MNase assays to ensure that the DNA lengths consistently fell within the 180–200 bp range (Fig. S4B). These DNA lengths are sufficient for linker histone H1 binding, in agreement with previous findings indicating that >170 bp is adequate for linker histone association (PMID: 26212454). 

This information has been incorporated into the main text and Methods section; 

On page 5, line 178, the sentence was added to read, “To prevent dissociation of H1.8 from nucleosomes during DNA fragmentation, the MNase concentration and the reaction time were optimized to generate DNA fragment lengths with 180–200 bp (Fig. S4B), which is adequate for linker histone association (PMID 26212454).”

On page 32, line 1192, the sentence was added to read, “To digest chromatin, MNase concentration and reaction time were tested on a small scale and optimized to the condition that produces 180-200 bp DNA fragments.”

(2) Co-associated proteins with H1-GFP nucleosome.

We now include mass spectrometry (MS) data for the proteins in the sucrose density gradient fraction 5 used for MagIC-cryo-EM analysis of GFP-H1.8-bound chromatin proteins as well as MS of proteins isolated with the corresponding MagIC-cryo-EM beads (Table S2 and updated Table S5). As the reviewer expected, HMG proteins (hmga2.L and hmga2.S in Table S2) were present in interphase sucrose gradient fraction 5, but their levels were less than 2% of H1.8. Accordingly, none of the known chromatin proteins besides histones and the nucleoplasmin were detected by MS in the GFP-nanobody MagIC-cryo-EM beads, including the FACT complex and PCNA, whose levels in the sucrose fraction were comparable to H1.8 (Table S2), suggesting that our MagIC-cryo-EM analysis was not meaningfully affected by HMG proteins and other chromatin proteins. Consistent with our interpretation, the structural features of H1.8bound nucleosomes isolated from interphase and metaphase chromosomes were essentially identical.

Reviewer #2 (Public review):

Summary:

The authors present a straightforward and convincing demonstration of a reagent and workflow that they collectively term "MagIC-cryo-EM", in which magnetic nanobeads combined with affinity linkers are used to specifically immobilize and locally concentrate complexes that contain a protein-of-interest. As a proof of concept, they localize, image, and reconstruct H1.8-bound nucleosomes reconstructed from frog egg extracts. The authors additionally devised an image-processing workflow termed "DuSTER", which increases the true positive detections of the partially ordered NPM2 complex. The analysis of the NPM2 complex {plus minus} H1.8 was challenging because only ~60 kDa of protein mass was ordered. Overall, single-particle cryo-EM practitioners should find this study useful.

Strengths:

The rationale is very logical and the data are convincing.

Weaknesses:

I have seen an earlier version of this study at a conference. The conference presentation was much easier to follow than the current manuscript. It is as if this manuscript had undergone review at another journal and includes additional experiments to satisfy previous reviewers. Specifically, the NPM2 results don't seem to add much to the main story (MagIC-cryo-EM), and read more like an addendum. The authors could probably publish the NPM2 results separately, which would make the core MagIC results (sans DusTER) easier to read.

We thank the reviewer for constructive comments. We regret to realize that the last portion of the result section, where we have described a detailed analysis of NPM2 structures, was erroneously omitted from the submission due to MS Word's formatting error. We hope that the inclusion of this section will justify the inclusion of the NPM2 analysis. Specifically, we decided to include NPM2 structures to demonstrate that our method successfully determined the structure that had never been reported. Conformational changes in the NPM family have been proposed in previous studies using techniques such as NMR, negative stain EM, and simulations, and these changes are thought to play a critical role in regulating NPM function (PMID: 25772360, 36220893, 38571760), but there has been a confusion in the literature, for example, on the substrate binding site and on whether NPM2 recognizes the substrate as a pentamer or decamer. Despite their low resolution, our new cryo-EM structures of NPM2 suggest that NPM2 recognizes the substrate as a pentamer, identifies potential substrate-binding sites, and indicates the mechanisms underlying NPM2 conformational changes. We believe that publishing these results will provide valuable insights into the NPM research field and help guide and inspire further investigations.

Reviewer #3 (Public review):

Summary:

In this paper, Arimura et al report a new method, termed MagIC-Cryo-EM, which refers to the method of using magnetic beads to capture specific proteins out of a lysate via, followed immunoprecipitation and deposition on EM grids. The so-enriched proteins can be analzyed structurally. Importantly, the nanoparticles are further functionalized with protein-based spacers, to avoid a distorted halo around the particles. This is a very elegant approach and allows the resolution of the stucture of small amounts of native proteins at atomistic resolution.

Here, the authors apply this method to study the chromatosome formation from nucleosomes and the oocyte-specific linker histone H1.8. This allows them to resolve H1.8-containing chromatomosomes from oocyte extract in both interphase and metaphase conditions at 4.3 A resolution, which reveal a common structure with H1 placed right at the dyad and contacting both entry-and exit linker DNA.

They then investigate the origin of H1.8 loss during interphase. They identify a nonnucleosomal H1.8-containing complex from interphase preparations. To resolve its structure, the authors develop a protocol (DuSTER) to exclude particles with ambiguous center, revealing particles with five-fold symmetry, that matches the chaperone NPM2. MS and WB confirms that the protein is present in interphase samples but not metaphase. The authors further separate two isoforms, an open and closed form that coexist. Additional densities in the open form suggest that this might be bound H1.8.

Strengths:

Together this is an important addition to the suite of cryoEM methods, with broad applications. The authors demonstrate the method using interesting applications, showing that the methods work and they can get high resolution structures from nucleosomes in complex with H1 from native environments.

Weaknesses:

The structures of the NPM2 chaperone is less well resolved, and some of the interpretation in this part seems only weakly justified.

We thank the reviewer for recognizing the significance of our methods and for constructive comments. We regret to realize that the last portion of the result section where we have described detailed analysis of NPM2 structures was erroneously omitted from the submission due to the MS word's formatting error. We hope that inclusion of this section will justify the inclusion of NPM2 analysis. Specifically, we agree that our NPM2 structures are low-resolution and that our interpretations may be revised as higher-resolution structures become available, although we believe that publishing these results will provide valuable insights into the NPM research field and also will illustrate the power of MagIC-cryo-EM and DuSTER. To respond to this criticism, the revised manuscript now clearly describes the limitations of our NPM2 structures while highlighting the key insights. In page 12 line 452, the sentence was added to read, “While DuSTER enables the structural analysis of NPM2 co-isolated with H1.8-GFP, the resulting map quality is modest, and the reported numerical resolution may be overestimated. Furthermore, only partial density for H1.8 is observed. Although structural analysis of small proteins is inherently challenging, it is possible that halo-like scattering further hinder high-resolution structural determination by reducing the S/N ratio. More detailed structural analyses of the NPM2-substrate complex will be addressed in future studies.

Reviewer #1 (Recommendations for the authors): 

(1) To assess the advantage provided by the new technique for imaging of isolated pure or enriched fractions of native chromatin, the nucleosome structure analysis should be matched by a proper biochemical characterization of the isolated nucleosomes. Nucleosome DNA size is known to greatly affect linker histone affinity and additional proteins like HMG may compete with linker histone for binding. SDS-PAGE of the sucrose gradient fractions (Fig. 3E) shows many nonhistone proteins where H1-GFP appears to be a minor component. However, the gradient fractions contain both bound and unbound proteins. I would suggest that a larger-scale pull-down using the same GFP antibodies and streptavidin beads should be conducted and the captured nucleosome DNA and proteins characterized. 

We addressed the concerns brought by the reviewer as following:

(1) DNA length

As the reviewer correctly pointed out, linker DNA length is critical for linker histone binding, and conventional ChIP protocols often result in DNA over-digestion to lengths of 140–150 bp. To minimize DNA over-digestion and structural damage, we have optimized a gentle chromosomal nucleosome purification protocol that enabled the cryoEM analysis of chromosomal nucleosomes (PMID: 34478647). This protocol involves DNA digestion with a minimal amount of MNase at 4ºC, producing nucleosomal DNA fragments of 180–200 bp. Additionally, before each chromatin extraction, we performed small-scale MNase assays to ensure that the DNA lengths consistently fell within the 180–200 bp range (Fig. S4B). These DNA lengths are sufficient for linker histone H1 binding, in agreement with previous findings indicating that >170 bp is adequate for linker histone association (PMID: 26212454). 

This information has been incorporated into the main text and Methods section. 

On page 5, line 178, the sentence was added to read, “To prevent dissociation of H1.8 from nucleosomes during DNA fragmentation, the MNase concentration and the reaction time were optimized to generate DNA fragment lengths with 180–200 bp (Fig. S4B), which is adequate for linker histone association (PMID 26212454).”

On page 32, line 1192, the sentence was added to read, “To digest chromatin, MNase concentration and reaction time were tested on a small scale and optimized to the condition that produces 180-200 bp DNA fragments.”

(2) Co-associated proteins with H1-GFP nucleosome.

We now include mass spectrometry (MS) data for the proteins in the sucrose density gradient fraction 5 used for MagIC-cryo-EM analysis of GFP-H1.8-bound chromatin proteins as well as MS of proteins isolated with the corresponding MagIC-cryo-EM beads (Table S2 and updated Table S5). As the reviewer expected, HMG proteins (hmga2.L and hmga2.S in Table S2) were present in interphase sucrose gradient fraction 5, but their levels were less than 2% of H1.8. Accordingly, none of known chromatin proteins besides histones and the nucleoplasmin were detected by MS in the GFP-nanobody MagIC-cryo-EM beads, including the FACT complex and PCNA, whose levels in the sucrose fraction were comparable to H1.8 (Table S2), suggesting that our MagIC-cryo-EM analysis was not meaningfully affected by HMG proteins and other chromatin proteins. Consistent with our interpretation, the structural features of H1.8bound nucleosomes isolated from interphase and metaphase chromosomes were essentially identical.

(2) A similar pull-down analysis with quantitation of NPM2 and GFP (in addition to analysis of sucrose gradient fractions) should be conducted to show whether the immune-selected particles do indeed contains a stoichiometric complex of H1.8 with NPM2.  

Proteins isolated using MagIC-cryo-EM beads were identified through mass spectrometry (Fig. 4D). The MS signal suggests that the molar ratio of NPM2 is higher than that of H1.8 or sfGFP. This observation is consistent with the idea that an NPM2 pentamer can bind between one and five H1.8-GFP molecules.

(3) The use of recombinant, bacterial produced H1.8- GFP and just one type of antibodies (GFP) are certain limitations of this work. These limitations as well as future steps needed to use antibodies specific for native antigens, such as histone variants and epigenetic modifications should be discussed.  

We clarified these points in the “Limitation of the study” section (page 12, line 420). The revised sections are indicated by the underlines below.

“While MagIC-cryo-EM is envisioned as a versatile approach suitable for various biomolecules from diverse sources, including cultured cells and tissues, it has thus far been tested only with H1.8-bound nucleosome and H1.8-bound NPM2, both using antiGFP nanobodies to isolate GFP-tagged H1.8 from chromosomes assembled in

Xenopus egg extracts after pre-fractionation of chromatin. To apply MagIC-cryo-EM for the other targets, the following factors must be considered: 1) Pre-fractionation. This step (e.g., density gradient or gel filtration) may be necessary to enrich the target protein in a specific complex from other diverse forms (such as monomeric forms, subcomplexes, and protein aggregates). 2) Avoiding bead aggregation. Beads may be clustered by targets (if the target complex contains multiple affinity tags or is aggregated), nonspecific binders, and the target capture modules. To directly apply antibodies that recognize the native targets and specific modifications, optimization to avoid bead aggregation will be important. 3) Stabilizing complexes. The target complexes must be stable during the sample preparation. Crosslink was necessary for the H1.8-GFP-bound nucleosome. 4) Loading the optimum number of targets on the bead. The optimal number of particles per bead differs depending on target sizes, as larger targets are more likely to overlap. For H1.8-GFP-bound nucleosomes, 500 to 2,000 particles per bead were optimal. We expect that fewer particles should be coated for larger targets.”

Reviewer #2 (Recommendations for the authors):  

General: 

Figures: Most of the figures have tiny text and schematic items (like Fig. 2B). To save readers from having to enlarge the paper on their computer screen, consider enlarging the smallest text & figure panels. 

We enlarged the text in the main figures.

Is it possible that the MagIC method also keeps more particles "submerged", i.e., away from the air:water interface? Does MagIC change the orientation distribution?  

In theory, the preferred orientation bias should be reduced in MagIC-cryo-EM, as particles are submerged, and the bias is thought to arise from particle accumulation at the air-water interface. However, while the preferred orientation appears to be mitigated, the issue is not completely resolved, as demonstrated in Author response image 1.

Author response image 1.

A possible explanation for the remaining preferred orientation bias in MagIC-cryo-EM data is that many particles are localized on graphene-water interfaces.

Consider adding a safety note to warn about possible pinching injuries when handling neodymium magnets. 

This is a good idea. We added a sentence in the method section (page 24, line 878), “The two pieces of strong neodymium magnets have to be handled carefully as magnets can leap and slam together from several feet apart.”

In the methods section, the authors state that the grids were incubated on magnets, followed by blotting and plunge freezing in the Vitrobot. Presumably, the blotting was performed in the absence of magnets. The authors may want to clarify this in the text. If so, can the authors speculate how the magnet-treated beads are better retained on the grids during blotting? Is it due to the induced aggregation and/or deposition of the nanobeads on the grid surface? 

In the limitation section (page 12 line 446), the sentence was added to read:

“The efficiency of magnetic bead capture can be further improved. In the current MagICcryo-EM workflow, the cryo-EM grid is incubated on a magnet before being transferred to the Vitrobot for vitrification. However, since the Vitrobot cannot accommodate a strong magnet, the vitrification step occurs without the magnetic force, potentially resulting in bead loss. This limitation could be addressed by developing a new plunge freezer capable of maintaining magnetic force during vitrification.”

In the method section (page 27 line 993), the sentence was modified. The revised sections are indicated by underlines.

“The grid was then incubated on the 40 x 20 mm N52 neodymium disc magnets for 5 min within an in-house high-humidity chamber to facilitate magnetic bead capture. Once the capture was complete, the tweezers anchoring the grid were transferred and attached to the Vitrobot Mark IV (FEI), and the grid was vitrified by employing a 2second blotting time at room temperature under conditions of 100% humidity.”

Do you see an extra density corresponding to the GFP in your averages?  

Since GFP is connected to H1.8 via a flexible linker, the GFP structure was observed in complex with the anti-GFP nanobody, separate from the H1.8-nucleosome and H1.8NPM2 complexes, as shown in Fig. S10.

Fig. 5 & Fig. S11: The reported resolutions for NPM2 averages were ~5Å but the densities appear - to my eyes - to resemble a lower-resolution averages.  

Although DuSTER enables the 3D structural determination of NPM2 co-isolated with H1-GFP, we recognize that the quality of the NPM2 map falls short of the standard expected for a typical 5 Å-resolution map. To appropriately convey the quality of the NPM2 maps, we have included the 3D FSC and local resolution map of the NPM2 structure (new Fig. S12). Furthermore, we have revised the manuscript to deemphasize the resolution of the NPM2 structure to avoid any potential misinterpretation.

Fig. 5D: The cartoon says: "less H1.8 on interphase nucleosome" and "more H1.8 on metaphase nucleosome". Please help the readers understand this conclusion with the gel in Fig. 3C and the population histograms in Fig. 3F. 

As depicted in Fig. 3A, we previously identified the preferential binding of H1.8 to metaphase nucleosomes (PMID: 34478647). In this study, to obtain sufficient H1.8bound nucleosomes for MagIC-cryo-EM, we used 2.5 times more starting material for interphase samples compared to M-phase samples. This discrepancy complicates the comparison of H1-GFP binding ratios in western blots. However, in GelCode^TM Blue staining (Fig. S4A), where both H1-GFP and histone bands are visible, the preferential binding of H1.8 to metaphase nucleosomes can be observed (See fractions 11 in interphase and metaphase).

Abstract - that removes low signal-to-noise ratio particles -> to exclude low signal-tonoise ratio particles; The term "exclude" is more accurate and is in the DuSTER acronym itself. 

We edited it accordingly. 

P1 - to reduce sample volume/concentration -> to lower the sample volume/concentration needed 

We edited it accordingly.

P1 - Flow from 1st to 2nd paragraph could be improved. It's abrupt. Maybe say that some forms of nucleoprotein complexes are rare, with one example being H1.8-bound nucleosomes in interphase chromatin? 

We have revised the text to address the challenges involved in the structural characterization of native chromatin-associated protein complexes. The revised text reads, “Structural characterization of native chromatin-associated protein complexes is particularly challenging due to their heterogeneity and scarcity: more than 300 proteins directly bind to the histone core surface, while each of these proteins is targeted to only a fraction of nucleosomes in chromatin.”

P2 - interacts both sides of the linker DNA -> interacts with both the entry and exit linker DNA 

We have edited it accordingly.

P2 - "from the chromatin sample isolated from metaphase chromosomes but not from interphase chromosomes" - meaning that the interphase nucleosomes don't have H1.8 densities at all, or that they do, but the H1.8 only interacts with one of the two linker DNAs? 

In our original attempt to analyze nucleosome structures assembled in Xenopus egg extracts without MagIC-cryo-EM, we were not able to detect the density confidently assigned to H1.8 in interphase chromatin samples. To avoid potential confusion, the revised text reads, “We were able to resolve the 3D structure of the H1.8-bound nucleosome isolated from metaphase chromosomes but not from interphase chromosomes(3). The resolved structure indicated that H1.8 in metaphase is most stably bound to the nucleosome at the on-dyad position, in which H1 interacts with both the entry and exit linker DNAs(21–24). This stable H1 association to the nucleosome in metaphase likely reflects its role in controlling the size and the shape of mitotic chromosomes through limiting chromatin accessibility of condensins(25), but it remains unclear why H1.8 binding to the nucleosome in interphase is less stable. Since the low abundance of H1.8-bound nucleosomes in interphase chromatin might have prevented us from determining their structure, we sought to solve this issue by enriching H1.8bound nucleoprotein complexes through adapting ChIP-based methods.”

P1, P2 - The logical leap from "by adapting ChIP-based methods" to MagIC is not clear. 

We addressed this point by revising the text as shown above.

P2 - "Intense halo-like noise" - This is an awkward term. These are probably the Fresnel fringes that arise from underfocus. I wouldn't call this phenomenon "noise". https://www.jeol.com/words/emterms/20121023.093457.php  

We re-phrased it as “halo-like scattering”.

P3 -It may help readers to explain how cryo-EM structures of the H1.8-associated interphase nucleosomes would differentiate from the two models in Fig. 3A.  

We have revised the introduction section (lines 43~75), including the corresponding paragraph to address the comments above, highlighting the motivation behind determining the structures of interphase and metaphase H1.8-associated nucleosomes. We hope the revisions are now clear.

P6 - "they were masked by background noise from the ice, graphene". I thought that graphene would be contribute minimal noise because it is only one-carbon-layer thick? 

That is a valid point. We have removed the term ‘graphene’ from the sentence.

P6 - What was the rationale to focus on particles with 60 - 80Å dimensions? 

We observed that 60–80 Å particles were captured by MagIC-cryo-EM beads, as numerous particles of this size were clearly visible in the motion-corrected micrographs surrounding the beads. To clarify this, we revised the sentence to read: 'Topaz successfully picked most of the 60–80 Å particles visible in the motion-corrected micrographs and enriched around the MagIC-cryo-EM beads (Figure S6A).

P7 - Please explain a technical detail about DuSTER: do independent runs of Topaz picks give particle centers than differ by up to ~40Å or is it that 2D classification gives particle centers that differ by up to ~40Å? Is it possible to distinguish these two possibilities by initializing CryoSPARC on two independent 2D classification jobs on the same set of Topaz picks?  

Due to the small particle size of NPM2, the former type is predominantly generated when Topaz fails to pick the particles reproducibly. The first cycle of DuSTER removes both former-type particles (irreproducibly picked particles) and latter-type particles (irreproducibly centered particles), while subsequent cycles specifically target and remove the latter type. We have added the following sentence to clarify this (page 7, line 249). The revised sections are indicated by underlines below: “To assess the reproducibility of the particle recentering during 2D classification, two independent particle pickings were conducted by Topaz so that each particle on the grid has up to two picked points (Figure 4A, second left panel). Some particles that only have one picked point will be removed in a later step. These picked points were independently subjected to 2D classification. After recentering the picked points by 2D classification, distances (D) between recentered points from the first picking process and other recentered points from the second picking process were measured. DuSTER keeps recentered points whose D are shorter than a threshold distance (D_TH). By setting D_TH = 20 Å, 2D classification results were dramatically improved in this sample; a five-petal flower-shaped 2D class was reconstructed (Figure 4B). This step also removes the particles that only have one picked point.“

P8 - NPM2 was introduced rather abruptly (it was used as an initial model for 3D refinement). I see NPM2 appear in the supplemental figures cited before the text in P8, but the significance of NPM2 was not discussed there. The authors seem to have made a logical leap that is not explained. 

We have removed the term NPM2 in P8.

P9 - "extra cryo-EM densities, which likely represent H1." This statement would be better supported if the resolution of the reconstruction was high enough to resolve H1specific amino acids in the "extra densities" protruding from the petals. 

We concurred and softened the statement to read “extra cryo-EM densities, which may represent H1.8,”

P9 - "Notably, extra cryo-EM densities, which likely represent H1.8, are clearly observed in the open form but much less in the closed form near the acidic surface regions proximal to the N terminus of beta-1 and the C terminus of beta-8 (Fig. 5A and 5B)."  It would be helpful to point out where the "extra densities" are in the figure for the open and closed form. Some readers may not be able to extrapolate from the single red arrow to the other extra densities. 

Thank you for your comment. We have pointed out the density in the Fig 5A as well.

P9 - "Supporting this idea, the acidic tract A1 (aa 36-40) and A2 (aa 120-140) are both implicated in the recognition of basic substrates such as core histones..."  Did this sentence get cut off in the next column?  

We apologize for our oversight on this error. Due to an MS Word formatting error, the sentences (lines 316–343) were hidden beneath a figure. We have retrieved the missing sentences:

“Supporting this idea, the acidic tract A1 (aa 36-40) and A2 (aa 120-140), which are both implicated in recognition of basic substrates such as core histones(43,50), respectively interact with and are adjacent to the putative H1.8 density (Figure 5B). In addition, the NPM2 surface that is in direct contact with the putative H1.8 density is accessible in the open form while it is internalized in the closed form (Figure 5C). This structural change of NPM2 may support more rigid binding of H1.8 to the open NPM2, whereas H1.8 binding to the closed form is less stable and likely occurs through interactions with the C-terminal A2 and A3 tracts, which are not visible in our cryo-EM structures.

In the aforementioned NPM2-H1.8 structures, for which we applied C5 symmetry during the 3D structure reconstruction, only a partial H1.8 density could be seen (Figure 5B). One possibility is that H1.8 structure in NPM2-H1.8 does not follow C5 symmetry. As the size of the NPM2-H1.8 complex estimated from sucrose gradient elution volume is consistent with pentameric NPM2 binding to a single H1.8 (Figure 3C and Table S3), applying C5 symmetry during structural reconstruction likely blurred the density of the monomeric H1.8 that binds to the NPM2 pentamer. The structural determination of NPM2-H1.8 without applying C5 symmetry lowered the overall resolution but visualized multiple structural variants of the NPM2 protomer with different degrees of openness coexisting within a NPM2-H1.8 complex (Figure S14), raising a possibility that opening of a portion of the NPM2 pentamer may affect modes of H1.8 binding. Although more detailed structural analyses of the NPM2-substrate complex are subject of future studies, MagIC-cryo-EM and DuSTER revealed structural changes of NPM2 that was co-isolated H1.8 on interphase chromosomes.

Discussion 

MagIC-cryo-EM offers sub-nanometer resolution structural determination using a heterogeneous sample that contains the target molecule at 1~2 nM, which is approximately 100 to 1000 times lower than the concentration required for conventional cryo-EM methods, including affinity grid approach(9–11).”

Reviewer #3 (Recommendations for the authors):  

All with regards to the NPM2 part: 

It would be great if the authors could provide micrographs where the particles are visible, in addition to the classes. 

The particles on the motion-corrected micrographs are available in Fig S9.

Also, the angular distribution in the SI looks very uniform. 

I also wonder, if the authors could indicate the local resolution for all structures. 

Could the authors provide the 3D FSC for NPM2?  

Although DuSTER enables the 3D structural determination of NPM2 co-isolated with H1-GFP, we recognize that the quality of the NPM2 map falls short of the standard expected for a typical 5 Å resolution map. To appropriately convey the quality of the NPM2 maps, we have included the 3D FSC and local resolution map of the NPM2 structure (new Fig. S12).

I really cannot see a difference between the open and closed forms. Looking at the models, I am skeptical that the authors can differentiate the two forms with the available resolution. Could they provide statistics that support their assignments? 

To better highlight the structural differences between the two forms, we added a new figure to compare the maps between open and closed forms (Fig S12J-K).

Also, the 'additional density' representing H1.8 in the NPM2 structures - I cannot see it. 

We pointed out the density with the red arrow in the revised Fig 5A.

Minor comments: 

Something is missing at the end of Results, just before the beginning of the Discussion.  The figure legend for Fig. S12 is truncated, so it is unclear what is going on 

We apologize for our oversight on this error. Due to an MS Word formatting error, the sentences (lines 316–343) were hidden beneath a figure. We have retrieved the missing sentences:

“Supporting this idea, the acidic tract A1 (aa 36-40) and A2 (aa 120-140), which are both implicated in recognition of basic substrates such as core histones(43,50), respectively interact with and are adjacent to the putative H1.8 density (Figure 5B). In addition, the NPM2 surface that is in direct contact with the putative H1.8 density is accessible in the open form while it is internalized in the closed form (Figure 5C). This structural change of NPM2 may support more rigid binding of H1.8 to the open NPM2, whereas H1.8 binding to the closed form is less stable and likely occurs through interactions with the C-terminal A2 and A3 tracts, which are not visible in our cryo-EM structures.

In the aforementioned NPM2-H1.8 structures, for which we applied C5 symmetry during the 3D structure reconstruction, only a partial H1.8 density could be seen (Figure 5B). One possibility is that H1.8 structure in NPM2-H1.8 does not follow C5 symmetry. As the size of the NPM2-H1.8 complex estimated from sucrose gradient elution volume is consistent with pentameric NPM2 binding to a single H1.8 (Figure 3C and Table S2), applying C5 symmetry during structural reconstruction likely blurred the density of the monomeric H1.8 that binds to the NPM2 pentamer. The structural determination of NPM2-H1.8 without applying C5 symmetry lowered the overall resolution but visualized multiple structural variants of the NPM2 protomer with different degrees of openness coexisting within a NPM2-H1.8 complex (Figure S14), raising a possibility that opening of a portion of the NPM2 pentamer may affect modes of H1.8 binding. Although more detailed structural analyses of the NPM2-substrate complex are subject of future studies, MagIC-cryo-EM and DuSTER revealed structural changes of NPM2 that was co-isolated H1.8 on interphase chromosomes.

Discussion 

MagIC-cryo-EM offers sub-nanometer resolution structural determination using a heterogeneous sample that contains the target molecule at 1~2 nM, which is approximately 100 to 1000 times lower than the concentration required for conventional cryo-EM methods, including affinity grid approach(9–11).”

Figure S13: I am not sure how robust these assignments are at this low resolution. Are these real structures or classification artifacts? It feels very optimistic to interpret these structures  

We agree that our NPM2 structures are low-resolution and that our interpretations may be revised as higher-resolution structures become available, although we believe that publishing these results will provide valuable insights into the NPM research field and also will illustrate the power of MagIC-cryo-EM and DuSTER. Conformational changes in the NPM family have been proposed in previous studies using techniques such as NMR, negative stain EM, and simulations, and these changes are thought to play a critical role in regulating NPM function (PMID: 25772360, 36220893, 38571760), but there has been a confusion in the literature, for example, on the substrate binding site and on whether NPM2 recognizes the substrate as a pentamer or decamer. Despite their low resolution, our new cryo-EM structures of NPM2 suggest that NPM2 recognizes the substrate as a pentamer, identify potential substrate-binding sites, and indicate the mechanisms underlying NPM2 conformational changes. We believe that publishing these results will provide valuable insights into the NPM research field and help guide and inspire further investigations. 

To respond to this criticism, we have revised the manuscript to clearly describe the limitations of our NPM2 structures while highlighting the key insights. On page 12, line 452, the sentence was added to read, “While DuSTER enables the structural analysis of NPM2 co-isolated with H1.8-GFP, the resulting map quality is modest, and the reported numerical resolution may be overestimated. Furthermore, only partial density for H1.8 is observed. Although structural analysis of small proteins is inherently challenging, it is possible that halo-like scattering further hinders high-resolution structural determination by reducing the S/N ratio. More detailed structural analyses of the NPM2-substrate complex will be addressed in future studies.”

eLife Assessment

The formation of the Z-ring at the time of bacterial cell division interests researchers working towards understanding cell division across all domains of life. The manuscript by Jasnin et al reports the cryoET structure of toroid assembly formation of FtsZ filaments driven by ZapD as the cross linker. The findings are important and have the potential to open a new dimension in the field, but the evidence to support these exciting claims is currently incomplete, mostly because of the suboptimal "resolution of the toroids", so in the absence of additional experiments, the interpretations would need to be toned down.

Reviewer #1 (Public review):

Summary:

The major result in the manuscript is the observation of the higher order structures in a cryoET reconstruction that could be used for understanding the assembly of toroid structures. The cross-linking ability of ZapD dimers result in bending of FtsZ filaments to a constant curvature. Many such short filaments are stitched together to form a toroid like structure. The geometry of assembly of filaments - whether they form straight bundles or toroid like structures - depends on the relative concentrations of FtsZ and ZapD.

Strengths:

In addition to a clear picture of the FtsZ assembly into ring-like structures, the authors have carried out basic biochemistry and biophysical techniques to assay the GTPase activity, the kinetics of assembly, and the ZapD to FtsZ ratio.

Weaknesses:

The discussion does not provide an overall perspective that correlates the cryoET structural organisation of filaments with the biophysical data. The current version has improved in terms of addressing this weakness and clearly states the lacuna in the model proposed based on the technical limitations.

Future scope of work includes the molecular basis of curvature generation and how molecular features of FtsZ and ZapD affect the membrane binding of the higher order assembly.

Reviewer #3 (Public review):

Summary:

Previous studies have analyzed the binding of ZapD to FtsZ and provided images of negatively stained toroids and straight bundles, where FtsZ filaments are presumably crosslinked by ZapD dimers. Toroids without ZapD have also been previously formed by treating FtsZ with crowding agents. The present study is the first to apply cryoEM tomography, which can resolve the structure of the toroids in 3D. This shows a complex mixture of filaments and sheets irregularly stacked in the Z direction and spaced radially. The most important interpretation would be to distinguish FtsZ filaments from ZapD crosslinks, This is less convincing. The authors seem aware of the ambiguity: "However, we were unable to obtain detailed structural information about the ZapD connectors due to the heterogeneity and density of the toroidal structures, which showed significant variability in the conformations of the connections between the filaments in all directions." Therefore, the reader may assume that the crosslinks identified and colored red are only suggestions, and look for their own structural interpretations. But readers should also note some inconsistencies in stoichiometry and crosslinking arrangements that are detailed under "weaknesses."

Strengths.

This is the first cryoEM tomography to image toroids and straight bundles of FtsZ filaments bound to ZapD. A strength is the resolution, which. at least for the straight bundles. is sufficient to resolve the ~4.5 nm spacing of ZapD dimers attached to and projecting subunits of an FtsZ filament. Another strength is the pelleting assay to determine the stoichiometry of ZapD:FtsZ (although this also leads to weaknesses of interpretation).

Weaknesses

The stoichiometry presents some problems. Fig. S5 uses pelleting to convincingly establish the stoichiometry of ZapD:FtsZ. Although ZapD is a dimer, the concentration of ZapD is always expressed as that of its subunit monomers. Fig. S5 shows the stoichiometry of ZapD:FtsZ to be 1:1 or 2:1 at equimolar or high concentrations of ZapD. Thus at equimolar ZapD, each ZapD dimer should bridge two FtsZ's, likely forming crosslinks between filaments. At high ZapD, each FtsZ should have it's own ZapD dimer. However, this seems contradicted by later statements in Discussion and Results. (1) "At lower concentrations of ZapD, .. toroids are the most prominent structures, containing one ZapD dimer for every four to six FtsZ molecules." Shouldn't it be one ZapD dimer for every two FtsZ? (2) "at the high ZapD concentration...a ZapD dimer binds two FtsZ molecules connecting two filaments." Doesn't Fig. S5 show that each FtsZ subunit has its own ZapD dimer? And wouldn't this saturate the CTD sites with dimers and thus minimize crosslinking?

A major weakness is the interpretation of the cryoEM tomograms, specifically distinguishing ZapD from FtsZ. The distinction of crosslinks seems based primarily on structure: long continuous filaments (which often appear as sheets) are FtsZ, and small masses between filaments are ZapD. The density of crosslinks seems to vary substantially over different parts of the figures. More important, the density of ZapD's identified and colored red seem much lower than the stoichiometry detailed above. Since the mass of the ZapD monomer is half that of FtsZ, the 1:1 stoichiometry in toroids means that 1/3 of the mass should be ZapD and 2/3 FtsZ. However, the connections identified as ZapD seem much fewer than the expected 1/3 of the mass. The authors conclude that connections run horizontally, diagonally and vertically, which implies no regularity. This seems likely, but as I would suggest that readers need to consider for themselves what they would identify as a crosslink.

In contrast to the toroids formed at equimolar FtsZ and ZapD, thin bundles of straight filaments are assembled in excess ZapD. Here the stoichiometry is 2:1, which would mean that every FtsZ should have a bound ZapD DIMER. The segmentation of a single filament in Fig. 5e seems to agree with this, showing an FtsZ filament with spikes emanating like a picket fence, with a 4.5 nm periodicity. This is consistent with each spike being a ZapD dimer, and every FtsZ subunit along the filament having a bound ZapD dimer. But if each FtsZ has its own dimer, this would seem to eliminate crosslinking. The interpretative diagram in Fig. 6, far right, which shows almost all ZapD dimers bridging two FtsZs on opposite filaments, would be inconsistent with this 2:1 stoichiometry.

In the original review I suggested a control that might help identify the structures of ZapD in the toroids. Popp et al (Biopolymers 2009) generated FtsZ toroids that were identical in size and shape to those here, but lacking ZapD. These toroids of pure FtsZ were generated by adding 8% polyvinyl chloride, a crowding agent. The filamentous substructure of these toroids in negative stain seemed very similar to that of the ZapD toroids here. CryoET of these toroids lacking ZapD might have been helpful in confirming the identification of ZapD crosslinks in the present toroids. However, the authors declined to explore this control.

Finally, it should be noted that the CTD binding sites for ZapD should be on the outside of curved filaments, the side facing the membrane in the cell. All bound ZapD should project radially outward, and if it contacted the back side of the next filament, it should not bind (because the CTD is on the front side). The diagram second to right in Fig. 6 seems to incorporate this abortive contact.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The major result in the manuscript is the observation of the higher order structures in a cryoET reconstruction that could be used for understanding the assembly of toroid structures. The crosslinking ability of ZapD dimers result in bending of FtsZ filaments to a constant curvature. Many such short filaments are stitched together to form a toroid like structure. The geometry of assembly of filaments - whether they form straight bundles or toroid like structures - depends on the relative concentrations of FtsZ and ZapD.

Strengths:

In addition to a clear picture of the FtsZ assembly into ring-like structures, the authors have carried out basic biochemistry and biophysical techniques to assay the GTPase activity, the kinetics of assembly, and the ZapD to FtsZ ratio.

Weaknesses:

The discussion does not provide an overall perspective that correlates the cryoET structural organisation of filaments with the biophysical data.

The crosslinking nature of ZapD is already established in the field. The work carried out is important to understand the ring assembly of FtsZ. However, the availability of the cryoET observations can be further analysed in detail to derive many measurements that will help validate the model, and obtain new insights.

We thank the reviewer for these insightful comments on our work. We have edited the manuscript to resolve and clarify most of the issues raised during the review process.

Reviewer #2 (Public Review):

Summary:

In this paper, the authors set out to better understand the mechanism by which the FtsZ-associated protein ZapD crosslinks FtsZ filaments to assemble a large-scale cytoskeletal assembly. For this aim, they use purified proteins in solution and a combination of biochemical, biophysical experiments and cryo-EM. The most significant finding of this study is the observation of FtsZ toroids that form at equimolar concentrations of the two proteins.

Strengths:

Many experiments in this paper confirm previous knowledge about ZapD. For example, it shows that ZapD promotes the assembly of FtsZ polymers, that ZapD bundles FtsZ filaments, that ZapD forms dimers and that it reduces FtsZ's GTPase activity. The most novel discovery is the observation of different assemblies as a function of ZapD:FtsZ ratio. In addition, using CryoEM to describe the structure of toroids and bundles, the paper provides some information about the orientation of ZapD in relation to FtsZ filaments. For example, they found that the organization of ZapD in relation to FtsZ filaments is "intrinsic heterogeneous" and that FtsZ filaments were crosslinked by ZapD dimers pointing in all directions. The authors conclude that it is this plasticity that allows for the formation of toroids and its stabilization. Unfortunately, a high-resolution structure of the protein organization was not possible. These are interesting findings that in principle deserve publication.

We thank the reviewer for this valuable assessment. We have made several changes to the manuscript to improve its readability and comprehensibility. In addition, we have addressed the reviewer’s main concerns in the point-by-point response below.

Weaknesses:

While the data is convincing, their interpretation has some substantial weaknesses that the authors should address for the final version of this paper.

We have addressed most of the aspects highlighted by the reviewer to improve the quality and comprehensibility of our results.

For example, as the authors are the first to describe FtsZ-ZapD toroids, a discussion why this has not been observed in previous studies would be very interesting, i.e. is it due to buffer conditions, sample preparation?

Several factors may explain the absence of observed toroidal structures in other studies. FtsZ is a highly dynamic protein, and its behavior varies significantly with different environmental conditions, as detailed in the literature. These environmental factors include pH, salt concentration, protein type, GTP levels, and the purification strategy used. Previous research has employed negative stain electron microscopy (EM) to visualize ZapD-FtsZ structures. It is important to note that FtsZ is sensitive to surface effects when it is bound to or adsorbed onto membranes (Mateos-Gil et al. 2019 FEMS Microbiol Rev - DOI: 10.1093/femsre/fuy039). Therefore, the adsorption of FtsZ and ZapD onto the EM grid may influence the formation of higher order structures. In this study, we used cryo-electron microscopy (cryo-EM) and cryo-electron tomography (cryo-ET) to visualize the 3D organization of ZapD-mediated structures. This approach allows us to avoid staining artifacts and the distortion of structures caused by adsorption or drying of the grid. In addition, we can resolve single filaments. Our buffer conditions also differ slightly from those in previous studies, which may significantly impact the behavior of FtsZ, as illustrated in Supplementary Fig. 3.

At parts of the manuscript, the authors try a bit too hard to argue for the physiological significance of these toroids. This, however, is at least very questionable, because: The typical diameter is in the range of 0.25-1.0 μm, which requires some flexibility of the filaments to be able to accommodate this. It's difficult to see how a FtsZ-ZapD toroid, which appears to be quite rigid with a narrow size distribution of 502 nm {plus minus} 55 nm could support cell division rather than stalling it at that cell diameter. which the authors say is similar to the E. coli cell.

The toroidal structures formed by FtsZ and ZapD, with their characteristics similar to those of the bacterial division system, are significant in physiological contexts and warrant further study. The connections mediated by Zaps are expected to play a crucial role in filament organization, which is vital for the machinery enabling cellular constriction. Therefore, characterizing these structures in vitro can provide insight into divisome stabilization, assembly and constriction mechanisms. While we acknowledge the limitations of in vitro systems and do not expect to see the same toroidal structures in vivo, the way ZapD decorates and connects FtsZ filaments in vitro may resemble the processes that occur in the division ring formed inside the cell. This study represents an initial effort to characterize these toroidal structures, which could inspire further research and potentially reveal their physiological relevance.

Regarding flexibility, it has been previously reported that an arrangement of loosely connected filaments forms the FtsZ ring. Our model is consistent with this observation despite the heterogeneity and density observed in the toroidal structures. We anticipate differences in vivo due to the high complexity of the cytoplasm, interactions with other cellular components, and attachment to the cell membrane, all of which would influence structural outcomes. However, our novel in vitro approach, which allows us to study FtsZ filament organization and connectivity – features that are challenging to explore in vivo and have not been thoroughly investigated before – has the potential to significantly advance our understanding of these structures. Consequently, these structures can aid our understanding of complex macrostructures in vivo, even if we have merely begun to scratch the surface of their characterization.

Regarding the size of the toroids, we hypothesize that it reflects an optimal condition based on our experimental setup in solution. In vivo, these conditions are altered by interactions with various division partners, attachment to the plasma membrane, and system contraction. 

We have better reformulated and edited the manuscript to discuss the potential physiological relevance of our toroidal structures.

For cell division, FtsZ filaments are recruited to the membrane surface via an interaction of FtsA or ZipA the C-terminal peptide of FtsZ. As ZapD also binds to this peptide, the question arises who wins this competition or where is ZapD when FtsZ is recruited to the membrane surface? Can such a toroidal structure of FtsZ filaments form on the membrane surface? Additional experiments would be helpful, but a more detailed discussion on how the authors think ZapD could act on membrane-bound filaments would be essential.

We appreciate this comment, which was indeed one of our main questions. The complexity of the division system raises many questions about the interaction of FtsZ with the plasma membrane. The competition between division components to interact with FtsZ and thus modulate its behavior is still largely unknown. FtsA and ZipA appear to have a greater affinity for the C-terminal domain (CTD) of FtsZ than ZapD. However, considering all FtsZ monomers forming a filament, we expect FtsZ filaments to interact with many different division partners. The ability of FtsZ to interact with many components is necessary to explain the current model of the system. According to this model, FtsZ filaments would be decorated by many different proteins, anchoring them to the membrane while crosslinking or promoting their disassembly in a spatiotemporally controlled manner. 

We tried experiments combining FtsA, ZipA, and ZapD on supported lipid membranes and liposomes. However, they proved difficult to perform. We expect similar results to those observed for ZapA (Caldas et al. 2019 Nat Commun - DOI: 10.1038/s41467-019-13702-4). However, competition between proteins for interaction with the CTD of FtsZ adds an extra layer of complexity, making exploring this issue attractive in the future. However, as remarkably pointed out by Reviewer 3, our cryo-ET data of straight bundles provide new insights into how ZapD-FtsZ structures can bind to the plasma membrane. In these straight bundles, the CTDs of two parallel FtsZ filaments are oriented upwards. They can bind the plasma membrane directly or the ZapDs, which decorate the FtsZ filaments from above instead of from the side, as suggested previously (Schumacher et al. 2017 J Biol Chem - DOI: 10.1074/jbc.M116.773192), allowing ZapDs to interact with the membrane.

The authors conclude that the FtsZ filaments are dynamic, which is essential for cell division. But the evidence for dynamic FtsZ filaments within these toroids seems rather weak, as it is solely the partial reassembly after addition of GTP. As ZapD significantly slows down GTP hydrolysis, I am not sure it's obvious to make this conclusion.

FtsZ filaments are dynamic, as they can reassemble into macrostructures relatively quickly. Decreased GTPase activity is a good indicator of the formation of lateral interactions between filaments. For instance, under crowding conditions, FtsZ also reduces its GTPase activity, although the bundles disassemble very slowly over time (González et al. 2003 J. Biol. Chem - DOI: 10.1074/jbc.M305230200). We measured the GTPase activity during the first 5 minutes after GTP addition, conditions under which toroidal structures and bundles remain fully assembled. However, we expect GTPase activity to recover as the macrostructures disassemble, considering the reassembly of macrostructures after GTP resupply, which suggests that FtsZ filaments remain active and dynamic.

On a similar note, on page 5 the authors claim that ZapD would transiently interact with FtsZ filaments. What is the evidence for this? They also say that this transient interaction could have a "mechanistic role in the functionality of FtsZ macrostructures." Could they elaborate?

We have rephrased the whole paragraph in the revised version to clarify matters (page 10, lines 2434):

“These results are consistent with the observation that ZapD interacts with FtsZ through its central hub, which provides additional spatial freedom to connect other filaments in different conformations. This flexibility allows different filament organizations and contributes to structural heterogeneity. In addition, these results suggest that these crosslinkers can act as modulators of the dynamics of the ring structure, spacing filaments apart and allowing them to slide in an organized manner. The ability of FtsZ to treadmill directionally, together with the parallel or antiparallel arrangement of short, transiently crosslinked filaments, is considered essential for the functionality of the Z ring and its ability to exert constrictive force34,36–38,50. Thus, Zap proteins can play a critical role in ensuring correct filament placement and stabilization, which is consistent with the toroidal structure formed by ZapD.”

The author should also improve in putting their findings into the context of existing knowledge. For example:

The authors observe a straightening of filament bundles with increasing ZapD concentration. This seems consistent with what was found for ZapA, but this is not explicitly discussed (Caldas et al 2019)

We have discussed this similarity in the revised version of this manuscript (page 12, line 40 - page 13, line 8):

“Understanding how the associative states of ZapA (as tetramers) and ZapD (as dimers), together with membrane tethering, influence the predominant structures formed in both systems is essential. The complexity of the division system raises important questions about the interaction dynamics between FtsZ and the plasma membrane. The competitive nature of the division components to engage with FtsZ and modulate its functionality remains to be thoroughly elucidated. It is important to note that FtsA and ZipA have a greater affinity for the C-terminal domain of FtsZ than ZapD. Our cryo-ET data on straight bundles provide new perspectives on how ZapD-FtsZ structures can effectively bind to the plasma membrane; in particular, the C-terminal domains of parallel FtsZ filaments are oriented upward, allowing direct membrane binding or interaction with ZapDs that reinforce these filaments from above, rather than from the side, as previously suggested.”

A paragraph summarizing what is known about the properties of ZapD in vivo would be essential: i.e., what has been found regarding its intracellular copy number, location and dynamics?

We thank the reviewer for this valuable suggestion. We describe the role of Zap proteins in vivo and the previous studies of ZapD in the introduction (page 2, lines 34 - page 3, line 17). Additionally, we added the estimated number of ZapD copies in the cell in the discussion (page 11, lines 2-7).

In the introduction, the authors write that "GTP binding and hydrolysis induce a conformational change in each monomer that modifies its binding potential, enabling them to follow a treadmilling behavior". This seems inaccurate, as shown by Wagstaff et al. 2022, the conformational change of FtsZ is not associated with the nucleotide state. In addition, they write that FtsZ polymerization depends on the GTPase activity. It would be more accurate to write that polymerization depends on GTP, and disassembly on GTPase activity.”

Following the reviewer's suggestions, we have adapted and corrected these text elements as follows (page 2, lines 7-9): 

“FtsZ undergoes treadmilling due to polymerization-dependent GTP hydrolysis, allowing the ring to exhibit its dynamic behavior.”

On page 2 they also write that "the mechanism underlying bundling of FtsZ filaments is unknown". I would disagree, the underlying mechanism is very well known (see for example Schumacher, MA JBC 2017), but how this relates to the large-scale organization of FtsZ filaments was not clear.

We thank the reviewer for this comment. We have corrected and clarified the related text accordingly (page 3, lines 11-12):

“…the link between FtsZ bundling, promoted by ZapD, and the large-scale organization of FtsZ filaments remains unresolved.”

The authors describe the toroid as a dense 3D mesh, how would this be compatible with the Z-ring and its role for cell division? I don't think this corresponds to the current model of the Z-ring (McQuillen & Xiao, 2020). Apart from the fact it's a ring, I don't think the organization of FtsZ obviously similar to the current of the Z-ring in the bacterial cell, in particular because it's not obvious how FtsZ filaments can bind ZapD and membrane anchors simultaneously.

We consider that the intrinsic characteristics of toroidal structures and the bacterial division ring have points in common. As indicated in the answer above, despite the differences and limitations that might result from an in vitro approach, the structures shown after ZapD crosslinking of FtsZ filaments can demonstrate intrinsic features occurring in vivo. The current model of the division ring consists of an arrangement of filaments loosely connected by crosslinkers in the center of the cell, forming a ring. This model is compatible with our findings, although many questions remain about the structural organization of the Z-ring in the cell.

Reviewer 3 has brought a compelling new perspective to interpreting our cryo-ET data: ZapD decorates FtsZ from above, allowing ZapD or FtsZ to bind to the plasma membrane. We have discussed this point in more detail below. In the case of straight bundles, this favors the stacking of straight FtsZ filaments, whereas in the case of toroids, ZapD can also bind FtsZ filaments laterally and diagonally, and it is this less compact arrangement that could enable FtsZ bending and toroid size adjustment. 

We have revised the text accordingly to incorporate the interpretation proposed by Reviewer 3 (page 12, lines 24-31):

“The current model of the division ring consists of an array of filaments loosely connected by crosslinkers at the center of the cell, forming a ring. This model is consistent with our findings, although many questions remain regarding the structural organization of the Z ring within the cell. ZapD binds to FtsZ from above, allowing either ZapD or FtsZ to interact with the plasma membrane. In straight bundles, this facilitates the stacking of straight FtsZ filaments, while for toroids, ZapD can also bind FtsZ filaments diagonally. This less compact arrangement could allow bending of the FtsZ filaments and adjustment of toroid size.”

The authors write that "most of these modulators" interact with FtsZ's CTP, but then later that ZapD is the only Zap protein that binds CTP. This seems to be inconsistent. Why not write that membrane anchors usually bind the CTP, most Zaps do not, but ZapD is the exception?

We thank the reviewer for this pertinent suggestion, which we have followed in the revised version of the manuscript (page 2, lines 19-22):

“Most of these modulators interact with FtsZ through its carboxy-terminal end, which modulates division assembly as a central hub.  ZapD is the only Zap protein known to crosslink FtsZ by binding its C-terminal domain, suggesting a critical Z ring structure stabilizing function.”

I also have some comments regarding the experiments and their analysis:

Regarding cryoET: the filaments appear like flat bands, even in the absence of ZapD, which further elongates these bands. Is this due to an anisotropic resolution? This distortion makes the conclusion that ZapD forms bi-spherical dimers unconvincing.

The missing wedge caused by the limited angular range of the tomography data generates an elongation of the structures by a factor of 2 along the Z axis. This feature is visible in the undecorated FtsZ filament data (Supplementary Fig. 10). The more pronounced elongation along the Z-axis observed in the presence of ZapD indicates the presence of ZapD to connect two parallel FtsZ filaments along the Z-axis (see Supplementary Figs. 8, 9 and 10). We do not have sufficient resolution to precisely resolve ZapD proteins from the FtsZ filaments in the Z-axis, but we also observed bispherical ZapDs in the XY plane (Fig. 4b-d). Unfortunately, our data do not allow for a more detailed characterization.

The authors say that the cryoET visualization provides crucial information on the length of the filaments within this toroid. How long are they? Could the authors measure it?

Measuring the length of single filaments is not trivial, given the dense, heterogeneous mesh promoted by ZapD crosslinking. We tried to identify and track them, but the density of filaments and connections made precise measurement very difficult. Nevertheless, we could identify the formation of these toroids by an arrangement of short filaments (Supplementary Fig. 11) instead of continuous circular filaments.

We have removed the following sentence text in the revised manuscript: “Visualization of ZapDmediated FtsZ toroidal structures by cryo-ET provided crucial information on the 3D organization, connectivity and length of filaments within the toroid.”

Regarding the dimerization mutant of ZapD: there is actually no direct confirmation that mZapD is monomeric. Did the authors try SEC MALS or AUC? Accordingly, the statement that dimerization is "essential" seems exaggerated (although likely true).

Unlike the wild-type ZapD protein, the mZapD mutant exists as a mixture of monomers (~15%) and dimers, as AUC assays performed at similar protein concentrations revealed. These results demonstrate that the mutant protein has a lower tendency to form dimers than the native ZapD protein. We have included the AUC data for mZapD in the supplementary material (Supp. Fig. 15a).

What do the authors mean that toroid formation is compatible with robust persistence length? I.e. What does robust mean? It was recently shown that FtsZ filaments are actually surprisingly flexible, which matches well the fact that the diameter of the Z-ring must continuously decrease during cell division (Dunajova et al Nature Physics 2023).

We have corrected this sentence in the revised version of the manuscript to improve clarity (page 11, lines 9-10): 

“The persistence length and curvature of FtsZ filaments are optimized for forming bacterial-sized ring structures.”

The authors claim that their observations suggest „that crosslinkers ... allows filament sliding in an organized fashion". As far as I know there is no evidence of filament sliding, as FtsZ monomers in living cells and in vitro are static.

Filament sliding may be one of the factors contributing to the force generation mechanisms involved in cell division (Nguyen et al. 2021 J Bacteriol - DOI: 10.1128/JB.00576-20). Our results indicate that ZapD can separate filaments, creating space between them and facilitating their organization.

Although the molecular dynamics of cell constriction are not yet fully understood, it is possible that filament sliding plays a role. If this is the case, the crosslinking of short FtsZ filaments in multiple directions by ZapD could provide the necessary flexibility to adjust the diameter of the constriction ring during bacterial division.

What is the „proto-ring FtsA protein"?

The proto-ring denotes the first molecular assembly of the Z-ring, which in E. coli consists of FtsZ, FtsA and ZipA (see, for example, Ortiz et al. 2016 FEMS Microbiol Rev - DOI: 10.1093/femsre/fuv040). To simplify matters, we have deleted the term “proto-ring” in the revised version of the MS.

The authors refer to „increasing evidence" for „alternative network remodeling mechanisms that do not rely on chemical energy consumption as those in which entropic forces act through diffusible crosslinkers, similar to ZapD and FtsZ polymers." A reference should be given, I assume the authors refer to the study by Lansky et al 2015 of PRC on microtubules. However, I am not sure how the authors made the conclusion that this applies to FtsZ and ZapD, on which evidence is this assumption based?

We refer to cytoskeletal network remodeling mechanisms independent of chemical energy consumption (Braun et al. 2016 Bioessays - DOI: 10.1002/bies.201500183) driven by entropic forces induced by macromolecular crowding agents or diffusible crosslinkers. The latter mechanism leads to an increase in filament overlap length and the contraction of filament networks. These mechanisms complement and act in synergy with energy-consuming processes (such as those involving nucleotide hydrolysis) to modulate actin- and microtubule-based cytoskeleton remodeling. Similarly, crosslinking proteins such as ZapD may contribute to remodeling the FtsZ division ring in the cell. 

We have revised the corresponding text of the manuscript accordingly (page 13, lines 16-24):  “In addition, our findings could greatly enhance the understanding of how polymeric cytoskeletal networks are remodeled during essential cellular processes such as cell motility and morphogenesis. Although conventional wisdom points to molecular motors as the primary drivers of filament remodeling through energy consumption, there is increasing evidence that there are alternative mechanisms that do not rely on such energy, instead harnessing entropic forces via diffusible crosslinkers. This approach may also be applicable to ZapD and FtsZ polymers, suggesting a promising avenue for optimizing conditions in the reverse engineering of the division ring to enhance force generation in minimally reconstituted systems aimed at achieving autonomous cell division.”

Some inconsistencies in supplementary figure 3: The normalized absorbances in panel a do not seem to agree with the absolute absorbance shown in panel e, i.e. compare maximum intensity for ZapD = 20 µM and 5 µM in both panels.

We have corrected these inconsistencies in the revised version.

It's not obvious to me why the structure formed by ZapD and FtsZ disassembles after some time even before GTP is exhausted, can the authors explain? As the structures disassemble, how is the "steadystate turbidity" defined? Do the structures also disassemble when they use a non-hydrolyzable analog of GTP?

In the presence of ZapD, FtsZ rapidly forms higher order polymers after the addition of GTP, as shown by turbidity assays at 320 nm (the formation of single- or double-stranded FtsZ filaments in the absence of ZapD does not produce a significant increase in turbidity). Macrostructures formed by FtsZ in the presence of ZapD, while more stable than FtsZ filaments (which rapidly disassemble following GTP consumption), are also dynamic. These assembly reactions are GTP-dependent and considerably modify polymer dynamics. In agreement with our results, previous studies have shown that high concentrations of macromolecular crowders (such as Ficoll or dextran) promote the formation of dynamic FtsZ polymer networks (González et al. 2003 J. Biol. Chem - DOI: 10.1074/jbc.M305230200). In this case, FtsZ GTPase activity was significantly retarded compared with FtsZ filaments, resulting in a decrease in GTPase turnover. Similar mechanisms may apply to assembly reactions in the presence of ZapD.

Parallel assembly studies replacing GTP with a slowly hydrolyzable GTP analog remain pending. We expect ZapD-containing FtsZ macrostructures to last assembled for longer but still disassemble upon GTP consumption, as occurs with the crowding-induced FtsZ polymer networks formed in the presence of nucleotide analogs.

Accordingly, we have revised the corresponding text to clarify matters (page 4, line 37 – page 5 line 7). 

Conclusion: Despite some weaknesses in the interpretation of their findings, I think this paper will likely motivate other structural studies on large scale assemblies of FtsZ filaments and its associated proteins. A systematic comparison of the effects of ZapA, ZapC and ZapD and how their different modes of filament crosslinking can result in different filament networks will be very useful to understand their individual roles and possible synergistic behavior.

We appreciate the reviewer's remarks and comments, which provided us with valuable information and helped us considerably improve the revised manuscript.

Reviewer #3 (Public Review):

Summary:

The authors provide the first image analysis by cryoET of toroids assembled by FtsZ crosslinked by ZapD. Previously toroids of FtsZ alone have been imaged only in projection by negative stain EM. The authors attempt to distinguish ZapD crosslinks from the underlying FtsZ filaments. I did not find this distinction convincing, especially because it seems inconsistent with the 1:1 stoichiometry demonstrated by pelleting. I was intrigued by one image showing straight filament pairs, which may suggest a new model for how ZapD crosslinks FtsZ filaments.

We thank the reviewer for these valuable comments, to which we have responded in detail below. 

Strengths:

(1) The first image analysis of FtsZ toroids by cryoET.

(2) The images are accompanied by pelleting assays that convincingly establish a 1:1 stoichiometry of FtsZ:ZapD subunits.

(3) Fig. 5 shows an image of a pair of FtsZ filaments crosslinked by ZapD. This seems to have higher resolution than the toroids. Importantly, it suggests a new model for the structure of FtsZ-ZapD that resolves previously unrecognized conflicts. (This is discussed below under weaknesses, because it is so far only supported by a single image.)

We thank the reviewer for this assessment and, in particular, for raising point 3, which provided a new perspective on the interpretation of our data. We have also included a new example of a straight bundle in Supplementary Fig. 13.

Weaknesses:

This paper reports a study by cryoEM of polymers and bundles assembled from FtsZ plus ZapD. Although previous studies by other labs have focused on straight bundles of filaments, the present study found toroids mixed with these straight bundles, and they focused most of their study on the toroids. In the toroids they attempt to delineate FtsZ filaments and ZapD crosslinks. A major problem here is with the stoichiometry. Their pelleting assays convincingly established a stoichiometry of 1:1, while the mass densities identified as ZapD are sparse and apparently well below the number of FtsZ (FtsZ subunits are not resolved in the reconstructions, but the continuous sheets or belts seem to have a lot more mass than the identified crosslinks.)  

Apart from the stoichiometry I don't find the identification of crosslinks to be convincing. It is missing an important control - cryoET of toroids assembled from pure FtsZ, without ZapD.

However, if I ignore these and jump to Fig. 5, I think there is an important discovery that resolves controversies in the present study as well as previous ones, controversies that were not even recognized. The controversy is illustrated by the Schumacher 2017 model (their Fig. 7), which is repeated in a simplified version in Fig. 1a of the present mss. That model has a two FtsZ filaments in a plane facing ZapD dimers which bridge them. In this planar model the C-terminal linker, and the ctd of FtsZ that binds ZapD facing each other and the ZapD in the middle, with. The contradiction arises because the C-terminus needs to face the membrane in order to attach and generate a bending force. The two FtsZ filaments in the planar model are facing 90{degree sign} away from the membrane. A related contradiction is that Houseman et al 2016 showed that curved FtsZ filaments have the C terminus on the outside of the curve. In a toroid the C termini should all be facing the outside. If the paired filaments had the C termini facing each other, they could not form a toroid because the two FtsZ filaments would be bending in opposite directions.

Fig. 5 of the present ms seems to resolve this by showing that the two FtsZ filaments and ZapD are not planar, but stacked. The two FtsZ filaments have their C termini facing the same direction, let's say up, toward the membrane, and ZapD binds on top, bridging the two. The spacing of the ctd binding sites on the Zap D dimer is 6.5 nm, which would fit the ~8 nm width of the paired filament complex observed in the present cryoEM (Fig S13). In the Schumacher model the width would be about 20 nm. Importantly, the stack model has the ctd of each filament facing the same direction, so the paired filaments could attach to the membrane and bend together (using ctd's not bound by ZapD). Finally, the new arrangement would also provide an easy way for the complex to extend from a pair of filaments to a sheet of three or four or more. A problem with this new model from Fig. 5 is that it is supported by only a single example of the paired FtsZ-ZapD complex. If this is to be the basis of the interpretation, more examples should be shown. Maybe examples could be found with three or four FtsZ filaments in a sheet.

We thank the reviewer for asking interesting questions and suggesting a compelling model for how ZapD could bind FtsZ filaments. Cryo-ET of straight bundles revealed that high ZapD density promotes vertical stacking of FtsZ filaments and decoration of FtsZ filaments by ZapD from above. In toroids, FtsZ filaments are vertically decorated by ZapD, which explains the high elongation of the filament structures observed, consisting of FtsZ-ZapD(-FtsZ) units. In addition, we observed a high abundance of diagonal connections between FtsZ filaments of different heights, revealing a certain flexibility/malleability of ZapD to link filaments that are not perfectly aligned vertically. This configuration could give rise to curved filaments and the overall toroid structure.

The manuscript proposes that ZapD can bind FtsZ filaments in different directions. However, it seems to have a certain tendency to bind to the upper part of FtsZ filaments, stacking them vertically or vertically with a lateral shift (Supplementary Fig. 9). We also observe lateral connections, although the features of the toroidal structures limit their visualization. This enables both the binding to the membrane by ZapD or FtsZ and the formation of higher order FtsZ polymer structures. 

In summary, ZapD is capable of linking FtsZ filaments in multiple directions, including from the upper part of the filaments as well as laterally or diagonally. At high concentrations of ZapD, the filaments become more compactly arranged, primarily stacking vertically, which results in the loss of curvature. In contrast, at lower concentrations of ZapD, the FtsZ filaments are less tightly packed, leading to curved filaments and an overall toroidal structure that may resemble the in vivo ring structures.

We have edited our manuscript to accommodate this hypothesis, including the abstract and the cryoET section (page 7, lines 5-16): 

“The isosurface confirmed the presence of extended structures along the Z-axis, well beyond the elongation expected from the missing wedge effect for single FtsZ filaments (for comparison, see Supplementary Fig. 10). The vertically extended structures appeared to correspond to filaments that were connected or decorated by additional densities along the Z-axis (Supplementary Fig. 9b). Importantly, these densities were only observed in the presence of ZapD (Supplementary Fig. 10b), suggesting that they represent ZapD connections (Fig. 3e and Supplementary Figs. 8e and 9b). We note that the resolution of the data is not sufficient to precisely resolve ZapD proteins from the FtsZ filaments in the Z-axis.

These results suggest that the toroids are constructed and stabilized by interactions between ZapD and FtsZ, which are mainly formed along the Z-axis but also laterally and diagonally.”

Page 7, lines 40-42: 

“Cryo-ET imaging of ZapD-mediated FtsZ toroidal structures revealed a preferential vertical stacking and crosslinking of short ZapD filaments, which are also crosslinked laterally and diagonally, allowing for filament curvature.”

And in the discussion (page 12, lines 27-31): 

“ZapD binds to FtsZ from above, allowing either ZapD or FtsZ to interact with the plasma membrane. In straight bundles, this facilitates the stacking of straight FtsZ filaments, while for toroids, ZapD can also bind FtsZ filaments diagonally. This less compact arrangement could allow bending of the FtsZ filaments and adjustment of the toroid size.”

What then should be done with the toroids? I am not convinced by the identification of ZapD as "connectors." I think it is likely that the ZapD is part of the belts that I discuss below, although the relative location of ZapD in the belts is not resolved. It is likely that the resolution in the toroid reconstructions of Fig. 4, S8,9 is less than that of the isolated pf pair in Fig. 5c.

We agree with the reviewer's interpretation that ZapD can attach to FtsZ filaments from both above and laterally. The data from the straight bundles, which are more clearly resolved due to their thinner structure, demonstrate that ZapD can decorate FtsZ filaments vertically. Additionally, the toroidal data supports the notion that ZapD can act as a crosslinker between filaments that are not perfectly vertical, allowing for lateral offsets (see, for example, Fig. 4d) or lateral connections (Fig. 4b). 

We recognize that the resolution and high density of structures in our cryo-ET data make it challenging to accurately annotate proteins or connectors. Despite this difficulty, we have made efforts to label and identify the ZapD proteins and connectors. We employed an arbitrary labeling method to assist with visual interpretation. However, we acknowledge that some errors may exist and that ZapD proteins were not labeled, particularly along the Z-axis, where the missing wedge limits our ability to distinguish between ZapD and FtsZ proteins (page 7, lines 8-13):

“The vertically extended structures appeared to correspond to filaments that were connected or decorated by additional densities along the Z-axis (Supplementary Fig. 9b). Importantly, these densities were only observed in the presence of ZapD (Supplementary Fig. 10b), suggesting that they represent ZapD connections (Fig. 3e and Supplementary Figs. 8e and 9b). We note that the resolution of the data is not sufficient to precisely resolve ZapD proteins from the FtsZ filaments in the Z-axis. We note that the resolution of the data is not sufficient to precisely resolve ZapD proteins from the FtsZ filaments in the Z-axis.”

We draw attention to the limitation of our manual segmentation in the text as follows (page 7, lines 20-24):

“We manually labeled the connecting densities in the toroid isosurfaces to analyze their arrangement and connectivity with the FtsZ filaments. The high density of the toroids and the wide variety of conformations of these densities prevented the use of subtomogram averaging to resolve their structure and spatial arrangement within the toroids.”

Importantly, If the authors want to pursue the location of ZapD in toroids, I suggest they need to compare their ZapD-containing toroids with toroids lacking ZapD. Popp et al 2009 have determined a variety of solution conditions that favor the assembly of toroids by FtsZ with no added protein crosslinker. It would be very interesting to investigate the structure of these toroids by the present cryoEM methods, and compare them to the FtsZ-ZapD toroids. I suspect that the belts seen in the ZapD toroids will not be found in the pure FtsZ toroids, confirming that their structure is generated by ZapD.

The only reported toroidal structure of E. coli FtsZ can be found in the literature by Popp et al. (2009 Biopolymers – DOI: 10.1002/bip.21136). It is important to note that methylcellulose (MC) must be added to the working solution to induce the formation of these structures, as FtsZ toroids do not form in the absence of MC. The mechanisms by which MC promotes this assembly process go beyond mere excluded volume effects due to crowding, as the concentration of MC used is very low (less than 1 mg/ml), which is below the typical crowding regime. This suggests that there are additional interactions between MC and FtsZ. Such complexities and secondary interactions prevent the use of this system as a reliable control for the FtsZ toroidal structures reported here. Alternatively, we also considered the toroidal structures of FtsZ from Bacillus subtilis (Huecas et al. 2017 Biophys J - DOI: 10.1016/j.bpj.2017.08.046) and Cyanobacterium synechocystis (Wang et al. 2019 J Biol Chem – DOI: 10.1074/jbc.RA118.005200). However, these structures do not serve as appropriate controls due to the structural and molecular differences between these FtsZ proteins.

Recommendations for the authors:  

Reviewing Editor:

While the three referees recognize and appreciate the importance of this work several technical and interpretational questions have been raised. There was a prolonged discussion amongst the three expert referees, and it was felt that the current version suffers from a number of problems that the authors need to consider. These are to do with 1. Stoichiometry of ZapD-FtsZ 2. the evidence for crosslinks 3. how the cryo-ET data correlates with the biophysical data 4. Physiological relevance of the elucidated structures. Please take note of the public reviews (strengths and weaknesses) as well as "Recommendations to the authors" sections below, if you choose to prepare a revision.

In reading the reviews very carefully (as well as while following the ensuing robust discussion between the referees) I noticed that all points raised are extremely important to be addressed / reconciled (with experiments and / or discussion) for this study to become an outstanding contribution to bacterial cell biology field. I would therefore urge you to consider these carefully and revise the manuscript accordingly.

We thank the editorial board and reviewers for their excellent work evaluating and reviewing our manuscript. Their constructive suggestions and comments have been taken into account in preparing the revised version. We have paid particular attention to the four points mentioned above by the reviewing editor. We hope that the new version and this point-by-point rebuttal letter will answer most of the questions and weaknesses raised by the reviewers.

Reviewer #1 (Recommendations for the authors):

Suggestions for improvement of the manuscript:

(1) ZapD to FtsZ ratio:

i) Page 3: Results section, paragraph 1:

FtsZ to ZapD shows a 1:2 ratio. How does this explain cross linking by a dimeric species, as this will be equivalent to a 1:1 ratio of FtsZ and ZapD? The crystal structure in the reference cited has FtsZ peptide bound only to one side of the dimer, however a crosslinking effect can happen only if FtsZ binds to both protomers of ZapD dimer. If the decoration is not uniform as given in the toroid model based on cryoET, this should lead to a model with excess of FtsZ in the toroid?

On page 3 of the original manuscript, we stated that the binding stoichiometry of ZapD to FtsZ was 2:1, based on estimates derived from sedimentation velocity experiments involving the unassembled GDP form of FtsZ. However, upon reanalyzing these experiments, we found that the previous characterization of the association mode was overly simplistic. We determined that there are two predominant molecular species of ZapD:FtsZ complexes in solution, which correspond to ZapD dimers bound to either one or two FtsZ monomers, resulting in stoichiometries of 2:1 and 1:1, respectively. The revised binding stoichiometry data for ZapD and GDP-FtsZ suggests the presence of 1:1 ZapD-FtsZ complexes which aligns with the idea that FtsZ polymers can be crosslinked by dimeric ZapD species. In mixtures where ZapD is present in excess over FtsZ, the crosslinking corresponds to 1:1 binding stoichiometries, leading to the formation of straight macrostructures. Conversely, when the concentration of ZapD is reduced in the reaction mixture, the resulting macrostructures take the form of toroids. In this scenario, there is an excess of FtsZ because only some of the FtsZ molecules within the polymers are crosslinked by ZapD dimers, resulting in a binding stoichiometry of approximately 0.4 ZapD molecules per FtsZ, as quantified by differential sedimentation experiments.

We have rewritten the corresponding texts in the revised version to explain these matters (page 4 lines 14-18):

“Sedimentation velocity analysis of mixtures of the two proteins revealed the presence of two predominant molecular species of ZapD:FtsZ complexes in solution. These complexes are compatible with ZapD dimers bound to one or two FtsZ monomers, corresponding to ZapD:FtsZ stoichiometries of 2:1 and 1:1, respectively (Supplementary Fig. 1a (III-IV)). This observation is consistent with the proposed interaction model.”

ii) How does 40 - 80 uM of ZapD correspond to a molar ratio of approximately 6?

It was a typo from previous versions. We have corrected it in the revised version. 

iii) The ratios of ZapD to FtsZ are different when described later in page 4 in the context of the toroid. Are these ratios relevant compared to the contradicting ratios mentioned later in page 4?

To clarify issues related to the binding of ZapD to FtsZ, we have rewritten the sections on ZapD binding stoichiometries to both FtsZ-GDP and FtsZ polymers in the presence of GTP (see page 4 lines 14-18 and page 5 lines 15-26).

iv) Supplementary Figure 5:

In the representative gel shown, the amount of ZapD in the pellet does not appear to be double compared to 10 and 30 uM concentrations. However, the estimated amount in the plot shown in panel (c) appears to indicate that that ZapD has approximately doubled at 30 uM compared to 10 uM. Please re-check the quantification.

Without prior staining calibration of the gels, there is no simple quantitative relationship between gel band intensities after Coomassie staining and the amount of protein in a band (Darawshe et al. 1993 Anal Biochem - DOI: 10.1006/abio.1993.1581). The latter point precludes a quantitative comparison of pelleting / SDS-PAGE data and analytical sedimentation measurements.

v) How can a consistent ratio being maintained be explained in an irregular structure of the toroid? The number of ZapD should be much less compared to FtsZ according to the model.

See answers to points i) and iii)

(2) GTPase activity and assembly/disassembly of toroids:

i) Page 3, Results section: last paragraph:

What is the explanation or hypothesis for decrease in GTPase activity upon ZapD binding? Given that FtsZ core is not involved in the interaction of the higher order assemblies, what is the probable reason on decrease in GTPase activity upon ZapA binding?

Excluded volume effects caused by macromolecular crowding, such as high concentrations of Ficoll or dextran, promote the formation of dynamic FtsZ polymer networks (González et al. 2003 J. Biol. Chem - DOI: 10.1074/jbc.M305230200). In these conditions, FtsZ GTPase activity is significantly slowed down compared to the activity observed in FtsZ filaments formed without crowding, leading to a decreased GTPase turnover rate. Similar mechanisms may also apply to assembly reactions in the presence of ZapD (see, for example, Durand-Heredia et al. 2012 J Bacteriol - DOI: 10.1128/JB.0017612).

ii) How is the decrease in GTPase activity compatible with dynamics of disassembly? Please substantiate on why disassembly is linked to transient interaction with ZapD. Shouldn't disassembly and transient interaction be linked to recovery of GTPase activity rates? 

iii) Does the decrease in GTPase activity imply a reduced turnover of disassembly of FtsZ to monomers? Hence, how is the reduction in turbidity related to the decrease in GTPase activity? How does the GTPase activity change with time? iv) How can the decrease in GTPase activity with increasing ZapD be explained?

We conducted GTPase activity assays within the first two minutes following GTP addition, a timeframe that promotes bundle formation. Previous studies, such as those by Durand-Heredia et al. (2012 J Bacteriol - DOI: 10.1128/JB.00176-12), have also indicated a reduction in GTPase activity during the initial moments of bundling. The reviewer’s suggestion that GTPase activity should recover after the disassembly of toroids is valid and warrants further investigation. To test this hypothesis, measuring GTPase activity over extended periods would be necessary. When comparing FtsZ filaments observed in vitro, we found that ZapD-containing FtsZ bundles exhibit decreased GTPase activity. Although we did not measure it directly, we anticipate a reduction in the rate of GTP exchange within the polymer, similar to the behavior of FtsZ bundles formed in the presence of crowders (González et al. 2003 J. Biol. Chem - DOI: 10.1074/jbc.M305230200), which also display a delay in GTPase activity. High levels of ZapD enhance bundling, which may explain the decrease in GTPase activity as ZapD levels increase.

(3) Treadmilling and FtsZ filament organisation:

If the FtsZ filaments are cross linked antiparallel, how can tread milling behaviour be explained? Doesn't tread milling imply a directionality of filament orientations in the FtsZ bundles?

Our model can only suggest filament alignment. The latter is compatible with parallel and antiparallel filament organization.

The correlation between observed effects on GTPase activity, treadmilling and ZapD interaction will provide an interesting insight to the model.

Establishing a detailed correlation among these three factors could yield valuable insights into the mechanisms and potential physiological implications of the structural organization of FtsZ polymers influenced by crosslinking proteins and ZapD. To precisely characterize these interactions, further time-resolved assays in solution and reconstituted systems would be necessary, which is beyond the scope of this study.

(4) Toroid dimensions and intrinsic curvature:

i) Page 4: What is the correlation between the toroid dimensions and the intrinsic curvature of the FtsZ filaments? Given the thickness of ~ 127 nm, please provide an explanation of how the intrinsic curvature of FtsZ is compatible with both the inner and outer diameters of 500 nm and 380 nm.

We added a paragraph for clarification (page 6, lines 20-24):

“Previous studies have shown different FtsZ structures at different concentrations and buffer conditions. FtsZ filaments are flexible and can generate different curvatures ranging from mini rings of ~24 nm to intermediate circular filaments of ~300 nm or toroids of ~500 nm in diameter (reviewed in Erickson and Osawa 2017 Subcell Biochem - DOI: 10.1007/978-3-319-53047-5_5, and Wang et al. 2019 J Biol Chem - DOI: 10.1074/jbc.RA119.009621). It is reasonable to assume that FtsZ filaments can accommodate the toroid shape promoted by ZapD crosslinking.”

ii) For the curvature of FtsZ filaments to be similar, the length of the filaments in the inner circles of the toroid have to be smaller than those in the outer circles? Is this true? Or are the FtsZ filaments of uniform length throughout?

Due to the limitations in the resolution of the toroidal structure, we could not accurately measure the length or curvature of the filaments. Considering the FtsZ flexibility, these filaments may exhibit various curvatures and lengths, as previously mentioned.

iii) Is the ZapD density uniform thought the inner and outer regions of the toroid?

The heterogeneity found in the structures suggests a difference in ZapD binding densities; however, we lack quantitative data to confirm this. The outer regions are likely more exposed to the attachment of free ZapDs in the surrounding environment, which leads to the recruitment of more ZapDs and the formation of straight bundles. Supplementary Fig. 7b (right) features a zoomed-in image of a toroid adorned with globular densities in the outer areas, which may correspond to ZapD oligomers. Similar characteristics appear in the straight filaments illustrated in the panels of this figure. However, these features are absent or present in significantly lower quantities in toroids with a 1:1 ratio and toroids formed under a 1:6 ratio, suggesting that the external decoration is due to ZapD saturation. Unfortunately, we cannot provide further details on the characteristics of these protein associations.

(5) Regular arrangement and toroid structure:

i) Page 4: last section, first sentence: What is meant by 'regular' arrangement here? The word regular will imply a periodicity, which is not a feature of the bundles.

We have rephrased the sentence in the revised manuscript as follows (page 5, lines 35-36): “Previous studies have visualized bundles with similar features using negative-stain transmission electron microscopy.”

ii) Similarly, page 6 first sentence mentions about a conserved toroid structure. Which aspects of the toroid structure are conserved and what are the other toroids that are compared with?

We noted several features that are conserved in the ZapD-mediated toroidal structures, including their diameter, thickness, height, and roundness, as shown in Fig. 2d-e and Supplementary Fig. 6b-c. However, the internal organization of the toroid does not exhibit a periodic or regular structure. We have rephrased this to say: “…resulting in a toroidal structure observed for the first time following the interaction between FtsZ and one of its natural partners in vitro.” (page 7, lines 42-43):

iii) Discussion, para 1, last sentence: How is the toroid structural correlated with the bacterial cell FtsZ ring? What do the authors mean by 'structural compatibility' with the ring?

The toroidal structures described in this work are consistent with the intermediate curved conformation of FtsZ polymers observed more generally across bacterial species and are likely to be part of the FtsZ structure responsible for constriction-force generation (Erickson and Osawa 2017 Subcell Biochem - DOI: 10.1007/978-3-319-53047-5_5). In the case of E. coli, if we assume an average of around 5000 FtsZ monomers in the polymeric form (two-thirds of the total found in dividing cells), this number of FtsZ molecules would be enough to encircle the cell around 6-8 times (considering the axial spacing between FtsZ monomers and the cell perimeter), which would be compatible with the structure adopting the form of a discontinuous toroidal assembly. 

The term “structural compatibility” could be confusing, so we have removed it from the revised text. 

iv) Discussion, para 2:

Resemblance with the division ring in bacterial cells is mentioned in paragraph 2, however the features that are compared to claim resemblance comes later in the discussion. It will be helpful to rearrange the sections so that these are presented together.

We have reorganized the sections following the reviewer’s suggestion.

(6) CryoET of toroid and interpretation of the tomogram:

i) Supplementary figure 10: It is not convincing that the indicated densities correspond to ZapD. Is the resolution and the quality of the tomogram sufficient to comment on the localisation of ZapD? It is challenging to see any interpretable difference between FtsZ filament dimers in 10a vs FtsZ+ZapD in panel (b).

We acknowledge that localizing ZapDs in the structure is a challenge due to the limited resolution of the cryo-ET data (page 7, lines 11-13, 21-24). We have manually labeled putative ZapDs in the data and have done our best to identify the structures reasonably while recognizing the limitations of the segmentation. We use different colors to guide the eye without clearly stating what is or is not a ZapD. However, filaments found in 1:1 and 1:6 ratio toroids have a clear difference in thickness to those observed in the absence of ZapD. The filaments in 1:0 ratio toroids provide a reasonable control for elongation due to the missing wedge and allow us to attribute the extra filament thickness to ZapD densities confidently (page 7, lines 5-12).

ii) How is it quantified that the elongation in Z is beyond the missing wedge effect? Please include the explanation for this in the methods or the relevant data as Supplementary figure panels.

The missing wedge effect causes an elongation by a factor of 2 along the Z-axis. This elongation is evident in the filaments of the 1:0 ratio toroids. Consequently, the elongation in the filaments of the 1:1 and 1:6 ratio toroids exceed that observed due to the missing wedge effect. We have also added this information to the methods section (page 17, lines 31-33).

iii) Segmentation analysis of the tomogram and many method details of analysis and interpretation of the tomography data has not been described. This is essential to understand the reliability of the interpretation of the tomography data.

We provided thresholds for volume extraction as isosurfaces and clarified how the putative ZapDs are colored in the revised methods section (page 17, line 24-30). However, we could not perform quantitative analysis of the segmented structures.

(7) Quantification of structural features of the toroid:

i) Page 5 last sentence mentions that it provides crucial information on the connectivity and length of the filaments. Is it possible to show a quantification of these features in the toroid models?

Based on our data, we hypothesize that ZapD crosslinks filaments by creating a network of short filaments rather than long ones. These short filaments assemble to form a complete ring. However, the current resolution of the data precludes precise quantification of this process.

In the revised version, we have changed this last sentence to put the emphasis on the crosslinking geometry instead (page 7, lines 40-43):

“Cryo-ET imaging of ZapD-mediated FtsZ toroidal structures revealed a preferential vertical stacking and crosslinking of short ZapD filaments, which are also crosslinked laterally and diagonally, allowing for filament curvature and resulting in a toroidal structure observed for the first time following the interaction between FtsZ and one of its natural partners in vitro.”

ii) In toroids with increasing concentrations, will it be possible to quantify the number of blobs which have been interpreted as ZapD? Is this consistent with the data of FtsZ to ZapD ratios?

These quantifications would assist in interpreting the data. However, due to the limited resolution of the data, we are reluctant to provide estimates.

iii) What is the average length of the filaments in the toroid? Can this be quantified from the tomography data? Similarly, can there be an estimation of curvature of the filaments from the data?

Unfortunately, the complexity of the toroidal structure and the limited resolution we achieved prevent us from providing accurate quantification. We attempted to track and measure the length of the filaments, but this proved challenging due to the high concentration of connections. Regarding curvature, the arrangement of the filaments into toroids makes it difficult to measure the curvature of each filament. Additionally, the filaments are not perfectly aligned, which suggests that there may be various curvatures present.

iv) What is the average distance between the FtsZ filaments in the toroid? Does this correlate with the ZapD dimensions, when a model has been interpreted as ZapD?

We measured the spacing (not the center-to-center distance) between filaments in the toroids and showed this in Supplementary Fig. 14b (sky blue). We observed that the distances are very similar to those found for straight bundles (light blue), with a slightly greater variability. We should point out here that the distances were measured in the XY plane to simplify the measurements.

v) What is the estimate of average inter-filament distances within the toroid? (Similar data as in Figure 13 for bundles?) When the distance between filaments is less, is the angle between ZapD and FtsZ filament axis different from 90 degrees? This might help in validation of interpretation of some of the blobs as ZapD.

The distances between the filaments presented in Supplementary Figure 14b include those for toroids (1:1 ratio, represented in sky blue) and straight bundles (1:6 ratio, shown in light blue). We focused solely on the distance between filaments in the XY plane and did not differentiate based on the connection angle. Although the distance may vary with changes in the angles between filaments, our data does not permit us to make any quantitative measurements regarding these variations.

vi) How does the inter filament distance in the toroids compare with the dimensions of ZapD dimers, in the toroids and bundles? Is there a role played by the FtsZ linker in deciding the spacing?

The dimension of a ZapD dimer is ~7 nm along the longest axis. Huecas et al. (2017 Biophys J - DOI: 10.1016/j.bpj.2017.08.046) estimated an interfilament distance of ~6.5-6.7 nm for toroids of FtsZ from Bacillus subtilis. These authors also observed a difference in this spacing as a function of the linker, assuming that linker length would modulate FtsZ-FtsZ interactions. We observe a similar spacing for double filaments (5.9 ± 0.8 nm) and a longer spacing in the presence of ZapD (7.88 ± 2.1 nm). Previous studies with ZapD did not measure the distance between filaments but hypothesized that distances of 6-12 nm are allowed based on the structure of the protein (Schumacher M. 2017 J Biol Chem - DOI: 10.1074/jbc.M116.773192). Longer linkers may also provide additional freedom to spread the filaments further apart and facilitate a higher degree of variability in the connections by ZapD. This discussion has been included in the revised text (page 6, line 10-18).

(8) Crosslinking by ZapD and toroid reorganisation by transient interactions:

i) Page 5, paragraph 2: Presence of putative ZapD decorating a single FtsZ': When ZapD is interacting with 2 FtsZ monomers within the same protofilament, it does not have any more valency to crosslink filaments. How do the authors propose that this can connect nearby filaments?

We thank the reviewer for raising this interesting question. We see examples of ZapD dimers binding a filament through only one of the monomers, occupying one valency of the interaction and leaving one of the monomers available for another binding. We expect to see higher densities of ZapD in the outer regions of toroids simply because there are no longer (or not as frequent) FtsZ filaments available to be attached and join the overall toroid structure. Assuming that a ZapD dimer could bind the same FtsZ filament, this region would not be able to connect to other nearby filaments via these interactions.

ii) Page 5: How are the authors coming up with the proposal of a reorganisation of toroid structures to a bundle? Given the extensive cross linking, a transition from a toroid to a bundle has to be a cooperative process and may not be driven by transient interactions. I would imagine that the higher concentration of ZapD will directly result in straight bundles because of the increased binding events of a dimer to one filament.

Theoretically, this is correct. A certain degree of cooperativity linked to multivalent interactions would also favor the establishment of other ZapD connections. Furthermore, the formation of these structures occurs relatively quickly, within the first two minutes following the addition of GTP. We observed various intermediate structures, ranging from sparse filament bundles to toroids and straight filaments. However, the limited data prevents us from proposing a model that eventually explains the formation of higher-order structures over time.

iii) Given such a highly cross-linked mesh, how can you justify transient interactions and loss of ZapD leading to disassembly? The possibility that ZapD can diffuse out of such a network seems impossible. Hence, what is the significance of a transient interaction? What is the basis of calling the interactions transient?

We have noted that the term “transient” used to define the interaction between ZapD and FtsZ seems to generate confusion. Therefore, we have decided to replace this term to improve the readability of our manuscript, which has been edited accordingly.

iv) Does the spacing between ZapD connections decide the curvature of the toroid?

The FtsZ linker connected to ZapD molecules could modulate filament spacing and curvature, as previously suggested (Huecas et al. 2017 Biophys J - DOI: 10.1016/j.bpj.2017.08.046; Sundararajan and Goley 2017 J Biol Chem - DOI: 10.1074/jbc.M117.809939, and Sundararajan et al. 2018 Mol Microbiol - DOI: 10.1111/mmi.14081). In our structures, we observe a mixture of curvatures in the internal organization of the toroid. Despite the flexibility of FtsZ, filaments have a preferred curvature that FtsZ would initially determine. However, the amount of ZapD connections will eventually force the filament structure to adapt and align with neighboring filaments, facilitating connections with more ZapDs. Thus, the binding density of ZapD molecules significantly impacts FtsZ curvature rather than the ZapD connections themselves. However, the molecular mechanism describing the link between ZapD binding and polymer curvature remains unsolved.

v) What is the difference in conditions between supplementary figure 6 and 12? Why is it that toroids are not observed in 12, for the same ratios?

Both figures show images of samples under the same conditions. At high ZapD concentrations in the sample, we observe a mixture of structures ranging from single filaments, bundles, toroids, and straight bundles. In Supplementary Fig. 6, we have selected images of toroids, while in Supplementary Fig. 12, we have focused on single and double filaments. We aim to compare similar structures at different ZapD concentrations.

(9) Correlation with in vivo observations:

What is the approximate ratio of ZapD to FtsZ concentrations in the cell? In this context, within a cell which one - a toroid or bundle - will be preferred?

Previous studies have estimated that E. coli cells contain approximately 5,000 to 15,000 FtsZ protein molecules, resulting in a concentration of around 3 to 10 µM (Rueda et al. 2003 J Bacteriol - DOI: 10.1128/JB.185.11.3344-3351.2003). Furthermore, only about two-thirds of these FtsZ molecules participate in forming the division ring (Stricker et al. 2002 PNAS - DOI: 10.1073/pnas.052595099). In contrast, ZapD is a low-abundance protein, with only around 500 molecules per cell (DurandHeredia et al. 2012 J Bacteriol - DOI: 10.1128/JB.00176-12), making it a relatively small fraction compared to the FtsZ molecules. Under these circumstances, toroidal structures are more likely to form than straight bundles, as the latter would require significantly higher concentrations of ZapD for proper assembly. We have added these considerations in the revised text (page 11, lines 1-7).

(10) Interpretation of mZapD results:

i) What is the experimental proof for weakened stability of the dimer? Rather than weakened stability, does this form a population of only monomeric ZapD or a proportion of non-functional or unfolded dimer? This requires to be shown by AUC or SEC to substantiate the claim of a weakened interface.

We have provided new AUC results indicating that mZapD is partially monomeric, which suggests a weakened dimerization interface (page 9, line 15-16 and Supp. Fig. 15a). The assays revealed no signs of protein aggregation.

ii) How does a weaker dimer result in thinner bundles and not toroids? A weaker dimer would imply that the number of ZapD linked to FtsZ will be less than the wild type, leading to less cross linking, which should lead to toroid formation rather than thinner bundles.

This observation provides the most plausible explanation. However, we did not detect any toroidal structures, even at high concentrations of mZapD. This finding indicates that a more potent dimerization interface is essential for promoting the formation of toroidal structures rather than merely the number of ZapD-FtsZ connections. mZapD presumably has a reduced affinity for FtsZ, which, along with a weaker binding interface, may explain mZapD's inability to facilitate toroid formation.

iii) This observation would imply that the geometry of the dimeric interaction plays a role in the bending of the FtsZ filaments into toroids? Please comment.

Our data suggest that the binding density of ZapD to FtsZ polymers is a crucial factor governing the transition from toroidal structures to straight bundles. Toroids form when the polymers have excess free FtsZ (that ZapD does not crosslink). Additional factors, such as the orientation of the interactions, the length of the flexible linker, and the strength of the ZapD dimerization interface, are likely to contribute to these structural reorganizations. However, our current data do not allow for further analysis, and future experiments will be necessary to address these questions.

(11) Curvature and plasticity of toroid:

i) What are the factors that stabilise curved protofilaments/toroid structures in the absence of a cross linker, based on earlier studies from B. subtilis. A comparison will be insightful. ii) What is the effect of the linker length between FtsZ globular domain and CTP in the toroid spacing?

Huecas et al. 2017 (Biophys J - DOI: 10.1016/j.bpj.2017.08.046) concluded that the disordered CTL of FtsZ serves as a spacer that modulates the self-organization of FtsZ polymers. They proposed that this intrinsically disordered CTL, which spans the gap between protofilament cores, provides approximately 70 Å of lateral spacing between the curved Bacillus subtilis FtsZ (BsFtsZ), forming toroidal structures. In contrast, the parallel filaments of tailless BsFtsZ mutants, which have a reduced spacing of 50 Å, will likely stick together, resulting in the straight bundles observed. In the full-length BsFtsZ filament, the flexibility allowed by the lateral association favors the coalescence of these curved protofilaments, leading to the formation of toroidal structures. 

The role of the C-terminal tail of FtsZ in E. coli is critical for its functionality (Buske and Levin 2012 J Biol Chem - DOI: 10.1074/jbc.M111.330324). However, its structural involvement in complex formations remains unclear. Research indicates that any disordered peptide between 43 and 95 amino acids in length can function as a viable linker, while peptides that are significantly shorter or longer impede cell division (Gardner et al. 2013 Mol Microbiol - DOI: 10.1111/mmi.12279). Studies in E. coli and B. subtilis suggest that intrinsically disordered CTLs play a role in determining FtsZ assembly and function in vivo, and this role is dependent on the length, flexibility, and disorder of the tails. These aspects still require further exploration.

iii) How is it concluded that the concentration of ZapD is modulating the behaviour of the toroid structure? ZapD as a molecule does not have much room for conformational flexibility beyond a few angstroms, in the absence of long flexible regions. Rather, shouldn't the linker length of FtsZ to the CTP decide the plasticity of the toroid?

The length and flexibility of the linker can significantly influence structural interactions. As previously mentioned, a longer linker will likely enhance the range of interaction distances and orientations. However, specific interaction of ZapD and FtsZ is stronger than non-specific electrostatic FtsZ-FtsZ interactions, and this is not solely due to the flexibility of the linker. Instead, it can modulate the formation of either a toroidal structure or straight bundles.

iv) "a minor free energy perturbation to bring about significant changes in the geometry of the fibers due to modifications in environmental conditions" - this sentence is not clear to me. How did the data described in the paper relate to minor free energy perturbations and how do environmental conditions affect this?

This sentence aimed to convey the notion of polymorphism in FtsZ polymers. We acknowledge that the original version may have been unclear, so we have removed it in the new version of the manuscript (page 12, lines 1-2).

(12) Missing controls:

i) Supplementary Figure 2a: Interaction between ZapD and FtsZ: what was the negative control used in this experiment? Use of FtsZ with the CTP deletion or ZapD specific mutations will help in confirming that the Kd estimation is indeed driven by a specific interaction.

Negative controls correspond to FtsZ and ZapD alone.

ii) In a turbidity measurement, how will you distinguish between ZapD mediated bundling, ZapD independent bundling and FtsZ filaments alone? Here again, having a data with non-interacting mutational partners will make the data more reliable.

The turbidity signal of individual proteins in the absence and presence of GTP is indistinguishable from that of the buffer. We have indicated this in the figure legend.

iii) Control experiments to show that mZapD is folded (see point below) and to indeed prove that it is monomeric is missing.

We have included the missing AUC data in the supplementary information (Supp Fig 15a).

Minor points:

-  Page 2, para 4: beta-sheet domain (instead of beta-strand)

Done.

-  Fig 2a and b: Why is a ratio mentioned in Figure 2a legend? I understood these images as individual proteins at 10 uM concentrations.

That was a typing error; it corresponds to two individual proteins at 10 µM concentrations. 

-  Fig 2. Y-axis - spelling of frequency (change in all figures where applicable)

Corrected.

-  Supplementary Figure 5: FtsZ 5 uM - change u to micro symbol. FtsZ - t is missing

Corrected. 

-  Molecular weight marker is xx. What does xx stand for?

Corrected. 

-  Fig 1: Units for GTPase activity on the y-axis is missing.

Done.

-  Suppl Fig 3: How was the normalisation carried out for the turbidity data?

We have explained it the revised methods section. 

-  Page 4, line 5: p missing in ZapD

Done. 

-  Page 5: paragraph 1, last sentence: stabilised or established?

Done.

-  Page 6: 3rd sentence from last: correct the sentence (one ZapD two FtsZ)

Corrected. 

-  Page 14: Fluorescence microscopy and FRAP experiments have not been described in the manuscript. Hence, these are not required in the methods.

Corrected. 

-  Please include representative gels of purified protein samples used in the assay for sample quality control.

Controls for each protein are shown in Supplementary Fig. 5a as “control samples” corresponding to 5 µM of each protein before centrifugation.

Reviewer #3 (Recommendations for the authors):

Fig. S2a confirms and quantitates the interaction of ZapD with FtsZ-GDP monomers by F.A. It shows a surprisingly high Kd of ~10 µM. This seems important but it is ignored in the overall interpretation. Fig. S2b (FCS) suggests an even weaker interaction, but this may reflect higher order aggregates.

As the reviewer points out, the interaction between ZapD and FtsZ in the GDP form is weak, consistent with the need for high concentrations of ZapD to form FtsZ macrostructures in the presence of GTP.

We did not observe the formation of ZapD aggregates, even at higher protein (Author response image 1A) and salt (Author response image 1B) concentrations.

Author response image 1.

A) Sedimentation velocity (SV) profiles of ZapD over a concentration range of 2 to 30 µM in 50 mM KCl, 5 mM MgCl2, Tris-HCl pH 7. B) SV profiles of ZapD at 10 µM in different ionic strength concentrations in buffer 50-500 mM KCl, 5 mM MgCl2, 50 mM Tris-HCl pH 7. Abs280 measurements were collected at 48,000 rpm and 20 ºC. 

Describing their assembly of toroids the authors state "Upon adding equimolar amounts of ZapD, corresponding to the subsaturating ZapD binding densities described in the previous section". My reading of Fig. 1b and S5 is that FtsZ is almost fully saturated at 1:1 concentration; In S5a at 5:5 µM about 25% of each is in the pellet, which is near 1:1 saturation. It is certainly >50% saturated. Shouldn't this be clarified to read "slightly substoichiometric. Of course, that undermines the identification of ZapD as such a substoichiometric number.

We have rephrased the sentence following the reviewer’s suggestions to clarify matters (page 5, lines 39-40).

The cryoET images in Fig. 3 are an average of five slices with a total thickness of 32 nm. The circular "short filaments..almost parallel" are therefore not single 5 nm diameter FtsZ filaments but must be alignment of filaments axially into sheets (or belts, the axial structure shown in Fig. S8e, discussed next). Importantly, the authors indicate "connections between filaments" by red arrows. This seems wrong for two reasons. (1) The "connections" are very sparse, and therefore not consistent with the near saturation of FtsZ by ZapD. (2) To show up in the 32 nm averaged slice, connections from multiple filaments would have to be aligned. Fig. 3e is a "view of the segmented toroidal structure." I think it shows sheets of filaments as noted above, and the suggested "crosslinks" are again very sparse and no more convincing.

We thank the reviewer for pointing this out. This was an error on our part, which we have corrected in the figure legend of the revised version of the manuscript. The tomographic slice shown in Fig. 3a is an average of 5 slices, each with a pixel size of 0.86 nm, corresponding to a pixel size of 4.31 nm. It therefore corresponds to the thickness of a single FtsZ filament. The few red arrows indicate lateral connections between filaments, and as discussed earlier, ZapDs also crosslinks FtsZ filaments vertically, giving rise to the elongated structures observed in the Z-direction.

All 3-D reconstructions and segmented renditions should have a scale bar. The axial cylindrical sheets seem to be confirmed and qualified in Fig. S8e. The cylindrical sheets are not continuous, but seem to consist of belt-like filaments that are ~8-10 nm wide in the axial direction. Adjacent belts are separated axially by ~5 nm gaps, and radially by 4-20 nm. The densest filaments in the projection image Fig. 3b are probably an axial superposition of 2-3 belts, while the lighter filaments may be individual belts.

Fig. 4 shows a higher number of crosslinks but nowhere near a 1:1 stoichiometry. Most importantly to me, the identification of crosslinks vs filaments seems completely arbitrary. For example, if one colored grey all of the densities I 4a right panel, I would have no way to duplicate the distinctions shown in red and blue. Even if we accept the authors' distinction, it does not provide much structural insight. Continuous bands or sheets are identified as FtsZ, without any resolution of substructure, and any density outside these bands is ZapD. The spots identified as ZapD seem randomly dispersed and much too sparse to include all the ~1:1 ZapD.

We appreciate the reviewer's comments. Scale bars are present in the tomographic slices but not in the 3D views, as these are perspective views, and it would be inappropriate to include scale bars. To provide context for the images, we added the dimensions of the toroids and toroid sections to the figure legends. 

As previously mentioned, the resolution of our data limits our ability to accurately segment ZapD densities, especially in the Z direction. In Fig. 4, we have done our best to segment the ZapD densities at the top and sides of the FtsZ filaments, but many densities have been missed. We have clarified this point in the text and in the figure legend. We have clarified this point in both the text and the figure legends. This preliminary annotated view is meant to help illustrate the formation of the toroids. In Fig. 3, we have labeled only a few arrows to highlight the lateral connections between the FtsZ filaments; however, there are many more connections than those indicated.

Fig. S12 explores the effect of increasing ZapD to 1:6, and the authors conclude "the high concentration of ZapD molecules increased the number of links between filaments and ultimately promoted the formation of straight bundles." However, the binding sites on FtsZ are already nearly saturated at 10:10.

We cannot assume that all FtsZ binding sites are present at a 1:1 ratio. Our pelleting assay confirms the presence of both proteins in the pellet, but we should be cautious about quantification due to the limitations of this technique. Based on our cryo-EM experiments, the amount of ZapD associated with these structures is much lower. We hypothesize that ZapD proteins sediment with the large FtsZ structures, acting as an external decoration for the toroids. A single ZapD monomer may be bound to multiple outer filaments of the structures, which could effectively increase the total µM concentration observed in the pelleting assay. This situation may explain the enrichment of ZapD in the pellet at high concentrations, when theoretically only a 1:1 ratio should be possible. We have observed external decorations of ZapD at high concentrations (see Supplementary Fig. 6). We believe that the pelleting assay simplifies the system and should be used to complement the cryo-EM images.

Minor points.

In the Intro "..to follow a treadmilling behavior, similar to that of actin filaments.9-13." These refs have little to do with treadmilling. I suggest: Wagstaff..Lowe mBio 2017; Du..Lutkenhaus PNAS 2018; Corbin Erickson BJ 2020; Ruis..Fernandez-Tornero Plos Biol 2022.

Following the reviewer’s suggestions, we have modified the references in the revised version. 

The authors responded to a query during review stating that the concentration of ZapD always refers to the monomer subunit. That seems certainly the case for Fig. S1, but the caption to Fig. 1a confuses the stoichiometry issue: "expecting (sic) at around 2:1 FtsZ:ZapD." Perhaps it could be clarified by stating that the Fig. shows only half the FtsZ's occupied. But in Fig. 1b the absorbance reaches its maximum at equimolar FtsZ and ZapD. That means that all FtsZ's are bound to a ZapD monomer. Why not draw the model in 1A show that? Fig. S5 is also consistent with this 1:1 stoichiometry. And this might be the place to contrast the planar model with the stacked model suggested by Fig. 5 where the two FtsZ filaments are ~8 nm apart, and the ZapD bridging them is on top.

We have revised the legend for Fig. 1a to improve its readability. In Fig. 1b, the absorbance data indicate that most FtsZ proteins form macrostructures; however, this does not imply that all FtsZ proteins are bound to ZapDs. Our findings demonstrate that this binding only occurs in the case of straight bundles.

It may help to note that some previous studies have expressed the concentration of ZapD as the dimer. E.g., Roach..Khursigara 2016 found maximal pelleting at FtsZ:ZapD(dimer) of 2:1 (their Fig. 3), completely consistent with the 1:1 FtsZ:ZapD(monomer) in the present study.

We recognize this discrepancy in the literature. Therefore, throughout the manuscript, the molar concentrations of both proteins are expressed in terms of the FtsZ and ZapD monomer species.

eLife Assessment

Combining experimental and computation approaches, this manuscript provides convincing evidence for a post-transcriptional mechanism that provides robust control over the protein expression level of RecB in E. coli. In addition to uncovering how DNA damage drives higher levels of RecB protein, this work also reveals important tenets for how broader mechanisms that suppress noise and underlie responsive tuning of protein levels can be achieved.

Reviewer #1 (Public review):

Summary:

In this study the authors use an elegant set of single-molecule experiments to assess the transcriptional and post-transcriptional regulation of RecB. The question stems from a previous observation from the same lab, that RecB protein levels are low and not induced under DNA damage. The authors first show that recB transcript levels are low and have a short half-live. They further show that RecB levels are likely regulated via translational control. They provide evidence for low noise in RecB protein levels across cells and show that the translation of the mRNA increases under double-strand break conditions. Authors identify Hfq binding sites in the recbcd operon and show that Hfq regulates the levels of RecB protein without changing the mRNA levels. They suggest that RecB translation is directly controlled by Hfq binding to mRNA, as mutating one of the binding sites has a direct effect on RecB protein levels.

The implication of Hfq in regulation of RecB translation is important, and suggests mechanisms of cellular response to DNA damage that are beyond the canonically studied mechanisms (such as transcriptional regulation by LexA). Data are clearly presented and the writing is direct and easy to follow. Overall, the study is well-designed and provides novel insights into the regulation of RecB, that is part of the complex required to process break ends.

Comments on revisions:

All my comments are addressed - I congratulate the authors on this excellent work.

Reviewer #2 (Public review):

Summary:

The authors carry out a careful and rigorous quantitative analysis of RecB transcript and protein levels at baseline and in response to DNA damage. Using single-molecule FISH and Halo-tagging in order to achieve sensitive measurements, they provide evidence that enhanced RecB protein levels in response to DNA damage are achieved through a post-transcriptional mechanism mediated by the La-like RNA binding protein, Hfq. In terms of biological relevance, the authors suggest that this mechanism provides a way to control the optimum level of RecB expression as both deletion and over-expression are deleterious. In addition, the proposed mechanism provides a new framework for understanding how transcriptional noise can be suppressed at the protein level.

Strengths:

Strengths of the manuscript include the rigorous approaches and orthogonal evidence to support the core conclusions, for example, the evidence that altering either Hfq or its recognition sequence on the RNA similarly enhance the protein to RNA ratio of RecB. The writing is clear and the experiments are well-controlled. The modeling approaches provide essential context to interpret the data, particularly given the small numbers of molecules per cell. The interpretations are careful and well supported. The findings

Weaknesses:

Future studies (and possibly new experimental tools) will be needed to provide further insight into the relevance of the findings to more subtle changes in RecB levels than that occurring in response to extensive DNA damage.

Reviewer #3 (Public review):

Summary:

The work by Kalita et al. reports regulation of RecB expression by Hfq protein in E.coli cell. RecBCD is an essential complex for DNA repair and chromosome maintenance. The expression level needs to be regulated at low level under regular growth conditions but upregulated upon DNA damage. Through quantitative imaging, the authors demonstrate that recB mRNAs and proteins are expressed at low level under regular conditions. While the mRNA copy number demonstrates high noise level due to stochastic gene expression, the protein level is maintained at a lower noise level compared to expected value. Upon DNA damage, the authors claim that the recB mRNA concentration is decreased, however RecB protein level is compensated by higher translation efficiency. Through analyzing CLASH data on Hfq, they identified two Hfq binding sites on RecB polycistronic mRNA, one of which is localized at the ribosome binding site (RBS). Through measuring RecB mRNA and protein level in the ∆hfq cell, the authors conclude that binding of Hfq to the RBS region of recB mRNA suppresses translation of recB mRNA. This conclusion is further supported by the same measurement in the presence of Hfq sequestrator, the sRNA ChiX, and the deletion of the Hfq binding region on the mRNA.

Strengths:

(1) The manuscript is well-written and easy to understand.<br /> (2) While there are reported cases of Hfq regulating translation of bound mRNAs, its effect on reducing translation noise is relatively new.<br /> (3) The imaging and analysis are carefully performed with necessary controls.

Comments on revisions:

The authors have addressed my previous concerns.

Author response:

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

Reviewer #2 (Public Review):

The authors make a compelling case for the biological need to exquisitely control RecB levels, which they suggest is achieved by the pathway they have uncovered and described in this work. However, this conclusion is largely inferred as the authors only investigate the effect on cell survival in response to (high levels of) DNA damage and in response to two perturbations - genetic knock-out or over-expression, both of which are likely more dramatic than the range of expression levels observed in unstimulated and DNA damage conditions.

In the discussion of the updated version of the manuscript, we have clarified the limits of our interpretation of the role of the uncovered regulation.

Lines 411-417: “It is worth noting that the observed decrease in cell viability upon DNA damage was detected for relatively drastic perturbations such as recB deletion and RecBCD overexpression. Verifying these observations in the context of more subtle changes in RecB levels would be important for further investigation of the biological role of the uncovered regulation mechanism. However, the extremely low numbers of RecB proteins make altering its abundance in a refined, controlled, and homogeneous across cells manner extremely challenging and would require the development of novel synthetic biology tools.”

Reviewer #3 (Public Review):

The major weaknesses include a lack of mechanistic depth, and part of the conclusions are not fully supported by the data.

(1) Mechanistically, it is still unclear why upon DNA damage, translation level of recB mRNA increases, which makes the story less complete. The authors mention in the Discussion that a moderate (30%) decrease in Hfq protein was observed in previous study, which may explain the loss of translation repression on recB. However, given that this mRNA exists in very low copy number (a few per cell) and that Hfq copy number is on the order of a few hundred to a few thousand, it's unclear how 30% decrease in the protein level should resides a significant change in its regulation of recB mRNA.

We agree that the entire mechanistic pathway controlling recB expression may be not limited to just Hfq involvement. We have performed additional experiments, proposed by the reviewer, suggesting that a small RNA might be involved (see below, response to comments 3&4). However, we consider that the full characterisation of all players is beyond the scope of this manuscript. In addition to describing the new data (see below), we expanded the discussion to explain more precisely why changes in Hfq abundance upon DNA damage may impact RecB translation. 

Lines 384-391: “A modest decrease (~30%) in Hfq protein abundance has been seen in a proteomic study in E. coli upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002). While Hfq is a highly abundant protein, it has many mRNA and sRNA targets, some of which are also present in large amounts (DOI: 10.1046/j.1365-2958.2003.03734.x). As recently shown, the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes, where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding (DOI: 10.1016/j.celrep.2020.02.016). In line with these findings, it is conceivable that even modest changes in Hfq availability could result in significant changes in gene expression, and this could explain the increased translational efficiency of RecB under DNA damage conditions. “

(2) Based on the experiment and the model, Hfq regulates translation of recB gene through binding to the RBS of the upstream ptrA gene through translation coupling. In this case, one would expect that the behavior of ptrA gene expression and its response to Hfq regulation would be quite similar to recB. Performing the same measurement on ptrA gene expression in the presence and absence of Hfq would strengthen the conclusion and model.

Indeed, based on our model, we expect PtrA expression to be regulated by Hfq in a similar manner to RecB. However, the product encoded by the ptrA gene, Protease III, (i) has been poorly characterised; (ii) unlike RecB, is located in the periplasm (DOI: 10.1128/jb.149.3.1027-1033.1982); and (iii) is not involved in any DNA repair pathway. Therefore, analysing PtrA expression would take us away from the key questions of our study.

(3) The authors agree that they cannot exclude the possibility of sRNA being involved in the translation regulation. However, this can be tested by performing the imaging experiments in the presence of Hfq proximal face mutations, which largely disrupt binding of sRNAs.

(4) The data on construct with a long region of Hfq binding site on recB mRNA deleted is less convincing. There is no control to show that removing this sequence region itself has no effect on translation, and the effect is solely due to the lack of Hfq binding. A better experiment would be using a Hfq distal face mutant that is deficient in binding to the ARN motifs.

We performed the requested experiments. We included this data in the manuscript in the supplementary figure (Figure S11), and our interpretation in the discussion.

Lines 354-378: “While a few recent studies have shown evidence for direct gene regulation by Hfq in a sRNA-independent manner (DOI: 10.1101/gad.302547.117; DOI: 10.1111/mmi.14799; DOI: 10.1371/journal.pgen.1004440; DOI: 10.1111/mmi.12961; DOI: 10.1038/emboj.2013.205), we attempted to investigate whether a small RNA could be involved in the Hfq-mediated regulation of RecB expression. We tested Hfq mutants containing point mutations in the proximal and distal sides of the protein, which were shown to disrupt either binding with sRNAs or with ARN motifs of mRNA targets, respectively [DOI: 10.1016/j.jmb.2013.01.006, DOI: 10.3389/fcimb.2023.1282258]. Hfq mutated in either proximal (K56A) or distal (Y25D) faces were expressed from a plasmid in a ∆hfq background. In both cases, Hfq expression was confirmed with qPCR and did not affect recB mRNA levels (Supplementary Figure S11b). When the proximal Hfq binding side (K56A) was disrupted, RecB protein concentration was nearly similar to that obtained in a ∆hfq mutant (Supplementary Figure S11a, top panel). This observation suggests that the repression of RecB translation requires the proximal side of Hfq, and that a small RNA is likely to be involved as small RNAs (Class I and Class II) were shown to predominantly interact with the proximal face of Hfq [DOI: 10.15252/embj.201591569]. When we expressed Hfq mutated in the distal face (Y25D) which is deficient in binding to mRNAs, less efficient repression of RecB translation was detected (Supplementary Figure S11a, bottom panel). This suggests that RecB mRNA interacts with Hfq at this position. We did not observe full de-repression to the ∆hfq level, which might be explained by residual capacity of Hfq to bind its recB mRNA target in the point mutant (Y25D) (either via the distal face with less affinity or via the lateral rim Hfq interface).”

Taken together, these results suggest that Hfq binds to recB mRNA and that a small RNA might contribute to the regulation although this sRNA has not been identified.

(5) Ln 249-251: The authors claim that the stability of recB mRNA is not changed in ∆hfq simply based on the steady-state mRNA level. To claim so, the lifetime needs to be measured in the absence of Hfq.

We measured recB lifetime in the absence of Hfq in a time-course experiment where transcription initiation was inhibited with rifampicin and mRNA abundance was quantified with RT-qPCR. The results confirmed that recB mRNA lifetime in hfq mutants is similar to the one in the wild type (Figure S7d, referred to the line 263 of the manuscript).

(6) What's the labeling efficiency of Halo-tag? If not 100% labeled, is it considered in the protein number quantification? Is the protein copy number quantification through imaging calibrated by an independent method? Does Halo tag affect the protein translation or degradation?

Our previous study (DOI: 10.1038/s41598-019-44278-0) described a detailed characterization of the HaloTag labelling technique for quantifying low-copy proteins in single E. coli cells using RecB as a test case. 

In that study, we showed complete quantitative agreement of RecB quantification between two fully independent methods: HaloTag-based labelling with cell fixation and RecB-sfGFP combined with a microfluidic device that lowers protein diffusion in the bacterial cytoplasm. This second method had previously been validated for protein quantification (DOI: 10.1038/ncomms11641) and provides detection of 80-90% of the labelled protein. Additionally, in our protocol, immediate chemical fixation of cells after the labelling and quick washing steps ensure that new, unlabelled RecB proteins are not produced. We, therefore, conclude that our approach to RecB detection is highly reliable and sufficient for comparing RecB production in different conditions and mutants.

The RecB-HaloTag construct has been designed for minimal impact on RecB production and function. The HaloTag is translationally fused to RecB in a loop positioned after the serine present at position 47 where it is unlikely to interfere with (i) the formation of RecBCD complex (based on RecBCD structure, DOI: 10.1038/nature02988), (ii) the initiation of translation (as it is far away from the 5’UTR and the beginning of the open reading frame) and (iii) conventional C-terminalassociated mechanisms of protein degradation (DOI: 10.15252/msb.20199208). In our manuscript, we showed that the RecB-HaloTag degradation rate is similar to the dilution rate due to bacterial growth. This is in line with a recent study on unlabelled proteins, which shows that RecB’s lifetime is set by the cellular growth rate (DOI: 10.1101/2022.08.01.502339).

Furthermore, we have demonstrated (DOI: 10.1038/s41598-019-44278-0) that (i) bacterial growth is not affected by replacing the native RecB with RecB-HaloTag, (ii) RecB-HaloTag is fully functional upon DNA damage, and (iii) no proteolytic processing of the RecB-HaloTag is detected by Western blot. 

These results suggest that RecB expression and functionality are unlikely to be affected by the translational HaloTag insertion at Ser-47 in RecB.

In the revised version of the manuscript, we have added information about the construct and discuss the reliability of the quantification.

Lines 141-152: “To determine whether the mRNA fluctuations we observed are transmitted to the protein level, we quantified RecB protein abundance with singlemolecule accuracy in fixed individual cells using the Halo self-labelling tag (Fig. 2A&B).

The HaloTag is translationally fused to RecB in a loop after Ser47(DOI: 10.1038/s41598-019-44278-0) where it is unlikely to interfere with the formation of RecBCD complex (DOI: 10.1038/nature02988), the initiation of translation and conventional C-terminal-associated mechanisms of protein degradation (DOI: 10.15252/msb.20199208). Consistent with minimal impact on RecB production and function, bacterial growth was not affected by replacing the native RecB with RecBHaloTag, the fusion was fully functional upon DNA damage and no proteolytic processing of the construct was detected (DOI: 10.1038/s41598-019-44278-0). To ensure reliable quantification in bacteria with HaloTag labelling, the technique was previously verified with an independent imaging method and resulted in > 80% labelling efficiency (DOI: 10.1038/s41598-019-44278-0, DOI: 10.1038/ncomms11641). In order to minimize the number of newly produced unlabelled RecB proteins, labelling and quick washing steps were followed by immediate chemical fixation of cells.”

Lines 164-168: “Comparison to the population growth rate [in these conditions (0.017 1/min)] suggests that RecB protein is stable and effectively removed only as a result of dilution and molecule partitioning between daughter cells. This result is consistent with a recent high-throughput study on protein turnover rates in E. coli, where the lifetime of RecB proteins was shown to be set by the doubling time (DOI: 10.1038/s41467-024-49920-8).”

(7) Upper panel of Fig S8a is redundant as in Fig 5B. Seems that Fig S8d is not described in the text.

We have now stated in the legend of Fig S8a that the data in the upper panel were taken from Fig 5B to visually facilitate the comparison with the results given in the lower panel. We also noticed that we did not specify that in the upper panel in Fig S9a (the data in the upper panel of Fig S9a was taken from Fig 5C for the same reason). We added this clarification to the legend of the Fig S9 as well.

We referred to the Fig S8d in the main text. 

Lines 283-284: “We confirmed the functionality of the Hfq protein expressed from the pQE-Hfq plasmid in our experimental conditions (Fig. S8d).”

Reviewer #1 (Recommendations For The Authors):

(1) Experimental regime to measure protein and mRNA levels.

(a) Authors expose cells to ciprofloxacin for 2 hrs. They provide a justification via a mathematical model. However, in the absence of a measurement of protein and mRNA across time, it is unclear whether this single time point is sufficient to make the conclusion on RecB induction under double-strand break.

In our experiments, we only aimed to compare recB mRNA and RecB protein levels in two steady-state conditions: no DNA damage and DNA damage caused by sublethal levels of ciprofloxacin. We did not aim to look at RecB dynamic regulation from nondamaged to damaged conditions – this would indeed require additional measurements at different time points. We revised this part of the results to ensure that our conclusions are stated as steady-state measurements and not as dynamic changes.

Line 203-205: “We used mathematical modelling to verify that two hours of antibiotic exposure was sufficient to detect changes in mRNA and protein levels and for RecB mRNA and protein levels to reach a new steady state in the presence of DNA damage.”

(b) Authors use cell area to account for the elongation under damage conditions. However, it is unclear whether the number of copies of the recB gene are similar across these elongated cells. Hence, authors should report mRNA and protein levels with respect to the number of gene copies of RecB or chromosome number as well.

Based on the experiments in DNA damaging conditions, our main conclusion is that the average translational efficiency of RecB is increased in perturbed conditions. We believe that this conclusion is well supported by our measurements and that it does not require information about the copy number of the recB gene but only the concentration of mRNA and protein. We did observe lower recB mRNA concentration upon DNA damage in comparison to the untreated conditions, which may be due to a lower concentration of genomic DNA in elongated cells upon DNA damage, as we mention in lines (221-223).

Our calculation of translation efficiency could be affected by variations of mRNA concentration across cells in the dataset. For example, longer cells that are potentially more affected by DNA damage could have lower concentrations of mRNA. We verified that this is not the case, as recB mRNA concentration is constant across cell size distribution (see the figure below or Figure S5a from Supplementary Information).

Therefore, we do not think that the measurements of recB gene copy would change our conclusions. We agree that measuring recB gene copies could help to investigate the reason behind the lower recB mRNA concentration under the perturbed conditions as this could be due to lower DNA content or due to shortage of resources (such as RNA polymerases). However, this is a side observation we made rather than a critical result, whose investigation is beyond the scope of this manuscript.

Author response image 1.

(2) RecB as a proxy for RecBCD. Authors suggest that RecB levels are regulated by hfq. However, how does this regulatory circuit affect the levels of RecC and RecD? Ratio of the three proteins has been shown to be important for the function of the complex.

A full discussion of RecBCD complex formation regulation would require a complete quantitative model based on precise information on the dynamic of the complex formation, which is currently lacking. 

We can however offer the following (speculative) suggestions assuming that all three subunits are present in similar abundance in native conditions (DOI: 10.1038/s41598019-44278-0 for RecB and RecC). As the complex is formed in 1:1:1 ratio (DOI: 10.1038/nature02988), we propose that the regulation mechanism of RecB expression affects complex formation in the following way. If the RecB abundance becomes lower than the level of RecC and RecD subunits, the complex formation would be limited by the number of available RecB subunits and hence the number of functional RecBCDs will be decreased. On the contrary, if the number of RecB is higher than the baseline, then, especially in the context of low numbers, we would expect that the probability of forming a complex RecBC (and then RecBCD) will be increased. Based on this simple explanation, we might speculate that regulation of RecB expression may be sufficient to regulate RecB levels and RecBCD complex formation. However, we feel that this argument is too speculative to be added to the manuscript. 

(3) Role of Hfq in RecB regulation. While authors show the role of hfq in recB translation regulation in non-damage conditions, it is unclear as to how this regulation occurs under damage conditions.

(a) Have the author carried out recB mRNA and protein measurement in hfqdeleted cells under ciprofloxacin treatment?

We attempted to perform experiments in hfq mutants under ciprofloxacin treatment. However, the cells exhibited a very strong and pleiotropic phenotype: they had large size variability and shape changes and were also frequently lysing. Therefore, we did not proceed with mRNA and protein quantification because the data would not have been reliable. 

(b) How do the authors propose that Hfq regulation is alleviated under conditions of DNA damage, when RecB translation efficiency increases?

We propose that Hfq could be involved in a more global response to DNA damage as follows. 

Based on a proteomic study where Hfq protein abundance has been found to decrease (~ 30%) upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002), we suggest that this could explain the increased translational efficiency of RecB. While Hfq is a highly abundant protein, it has many targets (mRNA and sRNA), some of which are also highly abundant. Therefore the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes (DOI: 10.1046/j.13652958.2003.03734.x), where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding. We reason that upon DNA damage, a moderate decrease in the Hfq protein abundance (30%) can lead to a similar competition among Hfq targets where high-affinity targets outcompete low-affinity ones as well as low-abundant ones (such as recB mRNAs). Thus, the regulation of lowabundant targets of Hfq by moderate perturbations of Hfq protein level is a potential explanation for the change in RecB translation that we have observed. Potential reasons behind the changes of Hfq levels upon DNA damage would be interesting to explore, however this would require a completely different approach and is beyond the scope of this manuscript.

We have modified the text of the discussion to explain our reasoning:

Lines 384-391: “A modest decrease (~30%) in Hfq protein abundance has been seen in a proteomic study in E. coli upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002). While Hfq is a highly abundant protein, it has many mRNA and sRNA targets, some of which are also present in large amounts (DOI: 10.1046/j.1365-2958.2003.03734.x). As recently shown, the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes, where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding (DOI: 10.1016/j.celrep.2020.02.016). In line with these findings, it is conceivable that even modest changes in Hfq availability could result in significant changes in gene expression, and this could explain the increased translational efficiency of RecB under DNA damage conditions.”

(c) Is there any growth phenotype associated with recB mutant where hfq binding is disrupted in damage and non-damage conditions? Does this mutation affect cell viability when over-expressed or under conditions of ciprofloxacin exposure?

We checked the phenotype and did not detect any difference in growth or cell viability affecting the recB-5 UTR* mutants either in normal conditions or upon exposure to ciprofloxacin. However, this is expected because the repair capacity is associated with RecB protein abundance and in this mutant, while translational efficiency of recB mRNA increases, the level of RecB proteins remains similar to the wild-type (Figure 5E).

Minor points:

(1) Introduction - authors should also discuss the role of RecFOR at sites of fork stalling, a likely predominant pathway for break generated at such sites.

The manuscript focuses on the repair of DNA double-strand breaks (DSBs). RecFOR plays a very important role in the repair of stalled forks because of single-strand gaps but is not involved in the repair of DSBs (DOI: 10.1038/35003501). We have modified the beginning of the introduction to mention the role of RecFOR. 

Lines 35-39: “For instance, replication forks often encounter obstacles leading to fork reversal, accumulation of gaps that are repaired by the RecFOR pathway (DOI: 10.1038/35003501) or breakage which has been shown to result in spontaneous DSBs in 18% of wild-type Escherichia coli cells in each generation (DOI: 10.1371/journal.pgen.1007256), underscoring the crucial need to repair these breaks to ensure faithful DNA replication.”

(2) Methods: The authors refer to previous papers for the method used for single RNA molecule detection. More information needs to be provided in the present manuscript to explain how single molecule detection was achieved.

We added additional information in the method section on the fitting procedure allowing quantifying the number of mRNAs per detected focus.

Lines 515-530: “Based on the peak height and spot intensity, computed from the fitting output, the specific signal was separated from false positive spots (Fig. S1a). To identify the number of co-localized mRNAs, the integrated spot intensity profile was analyzed as previously described (DOI: 10.1038/nprot.2013.066). Assuming that (i) probe hybridization is a probabilistic process, (ii) binding each RNA FISH probe happens independently, and (iii) in the majority of cases, due to low-abundance, there is one mRNA per spot, it is expected that the integrated intensities of FISH probes bound to one mRNA are Gaussian distributed. In the case of two co-localized mRNAs, there are two independent binding processes and, therefore, a wider Gaussian distribution with twice higher mean and twice larger variance is expected. In fact, the integrated spot intensity profile had a main mode corresponding to a single mRNA per focus, and a second one representing a population of spots with two co-localized mRNAs (Fig. S1b). Based on this model, the integrated spot intensity histograms were fitted to the sum of two Gaussian distributions (see equation below where a, b, c, and d are the fitting parameters), corresponding to one and two mRNA molecules per focus. An intensity equivalent corresponding to the integrated intensity of FISH probes in average bound to one mRNA was computed as a result of multiple-Gaussian fitting procedure (Fig. S1b), and all identified spots were normalized by the one-mRNA equivalent.

“

Reviewer #2 (Recommendations For The Authors):

Overall the work is carefully executed and highly compelling, providing strong support for the conclusions put forth by the authors.

One point: the potential biological consequences of the post-transcriptional mechanism uncovered in the work would be enhanced if the authors could 1) tune RecB protein levels and 2) directly monitor the role that RecB plays in generating single-standed DNA at DSBs.

We agree that testing viability of cells in case of tunable changes in RecB levels would be important to further investigate the biological role of the uncovered regulation mechanism. However, this is a very challenging experiment as it is technically difficult to alter the low number of RecB proteins in a controlled and homogeneous across-cell manner, and it would require the development of precisely tunable and very lowabundant synthetic designs. 

We did monitor real-time RecB dynamics by tracking single molecules in live E. coli cells in a different study (DOI: 10.1101/2023.12.22.573010) that is currently under revision. There, reduced motility of RecB proteins was observed upon DSB induction indicating that RecB is recruited to DNA to start the repair process.

eLife Assessment

In this detailed study, Cohen and Ben-Shaul characterized Accessory Olfactory Bulb (AOB) cell responses to various conspecific urine samples in female mice across the estrous cycle. The authors found that AOB cell responses varied depending on the strain and sex of the sample, but no clear differences were observed between estrous and non-estrous females. These findings provide convincing evidence that the AOB functions as a stable sensory relay, without directly modulating responses based on reproductive state, which supports the role of downstream brain regions in integrating reproductive state. Overall, this study provides valuable insights for researchers in the fields of olfaction and social neuroscience.

Reviewer #1 (Public review):

Summary:

In this detailed study, Cohen and Ben-Shaul characterized the AOB cell responses to various conspecific urine samples in female mice across the estrous cycle. The authors found that AOB cell responses vary with the strains and sexes of the samples. Between estrous and non-estrous females, no clear or consistent difference in responses was found. The cell response patterns, as measured by the distance between pairs of stimuli, are largely stable. When some changes do occur, they are not consistent across strains or male status. The authors concluded that AOB detects the signals without interpreting them. Overall, this study will provide useful information for scientists in the field of olfaction.

Strengths:

The study uses electrophysiological recording to characterize the responses of AOB cells to various urines in female mice. AOB recording is not trivial as it requires activation of VNO pump. The team uses a unique preparation to activate the VNO pump with electric stimulation, allowing them to record AOB cell responses to urines in anesthetized animals. The study comprehensively described the AOB cell responses to social stimuli and how the responses vary (or not) with features of the urine source and the reproductive state of the recording females. The dataset could be a valuable resource for scientists in the field of olfaction.

Weaknesses:

(1) The figures could be better labeled.

(2) For Figure 2E, please plot the error bar. Are there any statistics performed to compare the mean responses?

(3) For Figure 2D, it will be more informative to plot the percentage of responsive units.

(4) Could the similarity in response be explained by the similarity in urine composition? The study will be significantly strengthened by understanding the "distance" of chemical composition in different urine.

(5) If it is not possible for the authors to obtain these data first-hand, published data on MUPs and chemicals found in these urines may provide some clues.

(6) It is not very clear to me whether the female overrepresentation is because there are truly more AOB cells that respond to females than males or because there are only two female samples but 9 male samples.

(7) If the authors only select two male samples, let's say ICR Naïve and ICR DOM, combine them with responses to two female samples, and do the same analysis as in Figure 3, will the female response still be overrepresented?

(8) In Figure 4B and 4C, the pairwise distance during non-estrus is generally higher than that during estrus, although they are highly correlated. Does it mean that the cells respond to different urines more distinctively during diestrus than in estrus?

(9) The correlation analysis is not entirely intuitive when just looking at the figures. Some sample heatmaps showing the response differences between estrous states will be helpful.

Reviewer #2 (Public review):

Summary:

Many aspects of the study are carefully done, and in the grand scheme this is a solid contribution. I have no "big-picture" concerns about the approach or methodology. However, in numerous places the manuscript is unnecessarily vague, ambiguous, or confusing. Tightening up the presentation will magnify their impact.

Strengths:

(1) The study includes urine donors from males of three strains each with three social states, as well as females in two states. This diversity significantly enhances their ability to interpret their results.

(2) Several distinct analyses are used to explore the question of whether AOB MCs are biased towards specific states or different between estrus and non-estrus females. The results of these different analyses are self-reinforcing about the main conclusions of the study.

(3) The presentation maintains a neutral perspective throughout while touching on topics of widespread interest.

Weaknesses:

(1) Introduction:<br /> The discussion of the role of the VNS and preferences for different male stimuli should perhaps include Wysocki and Lepri 1991

(2) Results:<br /> a) Given the 20s gap between them, the distinction between sample application and sympathetic nerve trunk stimulation needs to be made crystal clear; in many places, "stimulus application" is used in places where this reviewer suspects they actually mean sympathetic nerve trunk stimulation.<br /> b) There appears to be a mismatch between the discussion of Figure 3 and its contents. Specifically, there is an example of an "adjusted" pattern in 3A, not 3B.<br /> c) The discussion of patterns neglects to mention whether it's possible for a neuron to belong to more than one pattern. For example, it would seem possible for a neuron to simultaneously fit the "ICR pattern" and the "dominant adjusted pattern" if, e.g., all ICR responses are stronger than all others, but if simultaneously within each strain the dominant male causes the largest response.

(3) Discussion:<br /> a) The discussion of chemical specificity in urine focuses on volatiles and MUPs (citation #47), but many important molecules for the VNS are small, nonvolatile ligands. For such molecules, the corresponding study is Fu et al 2015.<br /> b) "Following our line of reasoning, this scarcity may represent an optimal allocation of resources to separate dominant from naïve males": 1 unit out of 215 is roughly consistent with a single receptor. Surely little would be lost if there could be more computational capacity devoted to this important axis than that? It seems more likely that dominance is computed from multiple neuronal types with mixed encoding.

(4) Methods:<br /> a) Male status, "were unambiguous in most cases": is it possible to put numerical estimates on this? 55% and 99% are both "most," yet they differ substantially in interpretive uncertainty.<br /> b) Surgical procedures and electrode positioning: important details of probes are missing (electrode recording area, spacing, etc).<br /> c) Stimulus presentation procedure: Are stimuli manually pipetted or delivered by apparatus with precise timing?<br /> d) Data analysis, "we applied more permissive criteria involving response magnitude": it's not clear whether this is what's spelled out in the next paragraph, or whether that's left unspecified. In either case, the next paragraph appears to be about establishing a noise floor on pattern membership, not a "permissive criterion."<br /> e) Data analysis, method for assessing significance: there's a lot to like about the use of pooling to estimate the baseline and the use of an ANOVA-like test to assess unit responsiveness.<br /> But:<br /> i) for a specific stimulus, at 4 trials (the minimum specified in "Stimulus presentation procedure") kruskalwallis is questionable. They state that most trials use 5, however, and that should be okay.<br /> ii) the methods statement suggests they are running kruskalwallis individually for each neuron/stimulus, rather than once per neuron across all stimuli. With 11 stimuli, there is a substantial chance of a false-positive if they used p < 0.05 to assess significance. (The actual threshold was unstated.) Were there any multiple comparison corrections performed? Or did they run kruskalwallis on the neuron, and then if significant assess individual stimuli? (Which is a form of multiple-comparisons correction.)

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this detailed study, Cohen and Ben-Shaul characterized the AOB cell responses to various conspecific urine samples in female mice across the estrous cycle. The authors found that AOB cell responses vary with the strains and sexes of the samples. Between estrous and non-estrous females, no clear or consistent difference in responses was found. The cell response patterns, as measured by the distance between pairs of stimuli, are largely stable. When some changes do occur, they are not consistent across strains or male status. The authors concluded that AOB detects the signals without interpreting them. Overall, this study will provide useful information for scientists in the field of olfaction.

Strengths:

The study uses electrophysiological recording to characterize the responses of AOB cells to various urines in female mice. AOB recording is not trivial as it requires activation of VNO pump. The team uses a unique preparation to activate the VNO pump with electric stimulation, allowing them to record AOB cell responses to urines in anesthetized animals. The study comprehensively described the AOB cell responses to social stimuli and how the responses vary (or not) with features of the urine source and the reproductive state of the recording females. The dataset could be a valuable resource for scientists in the field of olfaction.

Weaknesses:

(1) The figures could be better labeled.

Figures will be revised to provide more detailed labeling.

(2) For Figure 2E, please plot the error bar. Are there any statistics performed to compare the mean responses?

We did not perform statistical comparisons (between the mean rates across the population). We will add this analysis and the corresponding error bars. 

(3) For Figure 2D, it will be more informative to plot the percentage of responsive units.

We will do it.

(4) Could the similarity in response be explained by the similarity in urine composition? The study will be significantly strengthened by understanding the "distance" of chemical composition in different urine.

We agree. As we wrote in the Discussion: “Ultimately, lacking knowledge of the chemical space associated with each of the stimuli, this and all the other ideas developed here remain speculative.”

A better understanding of the chemical distance is an important aspect that we aim to include in our future studies. However, this is far from trivial, as it is not chemical distance per se (which in itself is hard to define), but rather the “projection” of chemical space on the vomeronasal receptor neurons array. That is, knowledge of the chemical composition of the stimuli, lacking full knowledge of which molecules are vomeronasal system ligands, will only provide a partial picture. Despite these limitations, this is an important analysis which we would have done had we access to this data.

(5) If it is not possible for the authors to obtain these data first-hand, published data on MUPs and chemicals found in these urines may provide some clues.

Measurements about some classes of molecules may be found for some of the stimuli that we used here, but not for all. We are not aware of any single dataset that contains this information for any type of molecules (e.g., MUPs) across the entire stimulus set that we have used. More generally, pooling results from different studies has limited validity because of the biological and technical variability across studies. In order to reliably interpret our current recordings, it would be necessary to measure the urinary content of the very same samples that were used for stimulation. Unfortunately, we are not able to conduct this analysis at this stage.

(6) It is not very clear to me whether the female overrepresentation is because there are truly more AOB cells that respond to females than males or because there are only two female samples but 9 male samples.

It is true that the number of neurons fulfilling each of the patterns depends on the number of individual stimuli that define it. However, our measure of “over-representation” aims to overcome this bias, by using bootstrapping to reveal if the observed number of patterns is larger than expected by chance. We also note that more generally, the higher frequency of responses to female, as compared to male stimuli, is obtained in other studies by others and by us, also when the number of male and female stimuli is matched (e.g., Bansal et al BMC Biol 2021, Ben-Shaul et al, PNAS 2010, Hendrickson et al, JNS, 2008).

(7) If the authors only select two male samples, let's say ICR Naïve and ICR DOM, combine them with responses to two female samples, and do the same analysis as in Figure 3, will the female response still be overrepresented?

We believe that the answer is positive, but we can, and will perform this analysis to check.

(8) In Figure 4B and 4C, the pairwise distance during non-estrus is generally higher than that during estrus, although they are highly correlated. Does it mean that the cells respond to different urines more distinctively during diestrus than in estrus?

This is an important observation. For the Euclidean distance there might be a simple explanation as the distance depends on the number of units (and there are more units recorded in non-estrus females). However, this simple explanation does not hold for the correlation distance. A higher distance implies higher discrimination during the non-estrus stage, but our other analyses of sparseness and the selectivity indices do not support this idea. We note that absolute values of distance measures should generally be interpreted cautiously, as they may depend on multiple factors including sample size. Also, a small number of non-selective units could increase the correlation in responses among stimuli, and thus globally shift the distances. For these reasons, we focus on comparisons, rather than the absolute values of the correlation distances. In the revised manuscript, we will note and discuss this important observation.

(9) The correlation analysis is not entirely intuitive when just looking at the figures. Some sample heatmaps showing the response differences between estrous states will be helpful.

If we understand correctly, the idea is to show the correlation matrices from which the values in 4B and 4C are taken. We can and will do this, probably as a supplementary figure.

Reviewer #2 (Public review):

Summary:

Many aspects of the study are carefully done, and in the grand scheme this is a solid contribution. I have no "big-picture" concerns about the approach or methodology. However, in numerous places the manuscript is unnecessarily vague, ambiguous, or confusing. Tightening up the presentation will magnify their impact.

We will revise the text with the aim of tightening the presentation.

Strengths:

(1) The study includes urine donors from males of three strains each with three social states, as well as females in two states. This diversity significantly enhances their ability to interpret their results.

(2) Several distinct analyses are used to explore the question of whether AOB MCs are biased towards specific states or different between estrus and non-estrus females. The results of these different analyses are self-reinforcing about the main conclusions of the study.

(3) The presentation maintains a neutral perspective throughout while touching on topics of widespread interest.

Weaknesses:

(1) Introduction:

The discussion of the role of the VNS and preferences for different male stimuli should perhaps include Wysocki and Lepri 1991

Agreed. we will refer to this work in our discussion.

(2) Results:

a) Given the 20s gap between them, the distinction between sample application and sympathetic nerve trunk stimulation needs to be made crystal clear; in many places, "stimulus application" is used in places where this reviewer suspects they actually mean sympathetic nerve trunk stimulation.

In this study, we have considered both responses that are triggered by sympathetic trunk activation, and those that occur (as happens in some preparations) immediately following stimulus application (and prior to nerve trunk stimulation). An example of the latter Is provided in the second unit shown in Figure 1D (and this is indicated also in the figure legend). In our revision, we will further clarify this confusing point.

b) There appears to be a mismatch between the discussion of Figure 3 and its contents. Specifically, there is an example of an "adjusted" pattern in 3A, not 3B.

True. Thanks for catching this error. We will correct this.

c) The discussion of patterns neglects to mention whether it's possible for a neuron to belong to more than one pattern. For example, it would seem possible for a neuron to simultaneously fit the "ICR pattern" and the "dominant adjusted pattern" if, e.g., all ICR responses are stronger than all others, but if simultaneously within each strain the dominant male causes the largest response.

This is true. In the legend to Figure 3B, we actually write: “A neuron may fulfill more than one pattern and thus may appear in more than one row.”, but we will discuss this point in the main text as well.

(3) Discussion:

a) The discussion of chemical specificity in urine focuses on volatiles and MUPs (citation #47), but many important molecules for the VNS are small, nonvolatile ligands. For such molecules, the corresponding study is Fu et al 2015.

We fully agree. We will expand our discussion and refer to Fu et al.

b) "Following our line of reasoning, this scarcity may represent an optimal allocation of resources to separate dominant from naïve males": 1 unit out of 215 is roughly consistent with a single receptor. Surely little would be lost if there could be more computational capacity devoted to this important axis than that? It seems more likely that dominance is computed from multiple neuronal types with mixed encoding.

We agree, and we are not claiming that dominance, nor any other feature, is derived using dedicated feature selective neurons.  Our discussion of resource allocation is inevitably speculative. Our main point in this context is that a lack of overrepresentation does not imply that a feature is not important. We will revise our discussion to better clarify our view of this issue.

(4) Methods:

a) Male status, "were unambiguous in most cases": is it possible to put numerical estimates on this? 55% and 99% are both "most," yet they differ substantially in interpretive uncertainty.

This sentence is actually misleading and irrelevant. Ambiguous cases were not considered as dominant for urine collection. We only classified mice as dominant if they were “won” in the tube test and exhibited dominant behavior in the subsequent observation period in the cage. We will correct the wording in the revised manuscript.

b) Surgical procedures and electrode positioning: important details of probes are missing (electrode recording area, spacing, etc).

True. We will add these details.

c) Stimulus presentation procedure: Are stimuli manually pipetted or delivered by apparatus with precise timing?

They are delivered manually. We will clarify this as well.

d) Data analysis, "we applied more permissive criteria involving response magnitude": it's not clear whether this is what's spelled out in the next paragraph, or whether that's left unspecified. In either case, the next paragraph appears to be about establishing a noise floor on pattern membership, not a "permissive criterion."

True, the next paragraph is not the explanation for the more permissive criteria. The more permissive criteria involving response magnitude are actually those described in Figure 3A and 3B. The sentence that was quoted above merely states that before applying those criteria, we had also searched for patterns defined by binary designation of neurons as responsive, or not responsive, to each of the stimuli (this is directly related to the next comment below). Using those binary definitions, we obtained a very small number of neurons for each pattern and thus decided to apply the approach actually used and described in the manuscript.

e) Data analysis, method for assessing significance: there's a lot to like about the use of pooling to estimate the baseline and the use of an ANOVA-like test to assess unit responsiveness.

But:

i) for a specific stimulus, at 4 trials (the minimum specified in "Stimulus presentation procedure") kruskalwallis is questionable. They state that most trials use 5, however, and that should be okay.

The number of cases with 4 trials is truly a minority, and we will provide the exact numbers in our revision.

ii) the methods statement suggests they are running kruskalwallis individually for each neuron/stimulus, rather than once per neuron across all stimuli. With 11 stimuli, there is a substantial chance of a false-positive if they used p < 0.05 to assess significance. (The actual threshold was unstated.) Were there any multiple comparison corrections performed? Or did they run kruskalwallis on the neuron, and then if significant assess individual stimuli? (Which is a form of multiple-comparisons correction.)

First, we indeed failed to mention that our criterion was 0.05. We will correct that in our revision. We did not apply any multiple comparison measures. We consider each neuron-stimulus pair as an independent entity, and we are aware that this leads to a higher false positive rate. On the other hand, applying multiple comparisons would be problematic, as we do not always use the same number of stimuli in different studies. Applying multiple comparison corrections would lead to different response criteria across different studies. Notably, most, if not all, of our conclusions involve comparisons across conditions, and for this purpose we think that our procedure is valid. We do not attach any special meaning to the significance threshold, but rather think of it as a basic criterion that allows us to exclude non-responsive neurons, and to compare frequencies of neurons that fulfill this criterion.

eLife Assessment

Pinho et al use in vivo calcium imaging and chemogenetic approaches to examine the involvement of hippocampal sub-regions across the different stages of a sensory preconditioning task in mice. They find convincing evidence for sensory preconditioning in male mice. They also find that, in these mice, CaMKII-positive neurons in the dorsal hippocampus: (1) encode the audio-visual association that forms in stage 1 of the task, and (2) retrieve/express sensory preconditioned fear to the auditory stimulus at test. These findings are supported by evidence that ranges from incomplete to convincing. The study will be valuable to researchers in the field of learning and memory.

Reviewer #1 (Public review):

Summary:

The study by Pinho et al. presents a novel behavioral paradigm for investigating higher-order conditioning in mice. The authors developed a task that creates associations between light and tone sensory cues, driving mediated learning. They observed sex differences in task acquisition, with females demonstrating faster-mediated learning compared to males. Using fiber photometry and chemogenetic tools, the study reveals that the dorsal hippocampus (dHPC) plays a central role in encoding mediated learning. These findings are crucial for understanding how environmental cues, which are not directly linked to positive/negative outcomes, contribute to associative learning. Overall, the study is well-designed, with robust results, and the experimental approach aligns with the study's objectives.

Strengths:

(1) The authors develop a robust behavioral paradigm to examine higher-order associative learning in mice.

(2) They discover a sex-specific component influencing mediated learning, with females exhibiting enhanced learning abilities.

(3) Using fiber photometry and chemogenetic techniques, the authors identify the dorsal hippocampus but not the ventral hippocampus, which plays a crucial for encoding mediated learning.

Weaknesses:

(1) The study would be strengthened by further elaboration on the rationale for investigating specific cell types within the hippocampus.

(2) The analysis of photometry data could be improved by distinguishing between early and late responses, as well as enhancing the overall presentation of the data.

(3) The manuscript would benefit from revisions to improve clarity and readability.

Reviewer #2 (Public review):

Summary:

Pinho et al. developed a new auditory-visual sensory preconditioning procedure in mice and examined the contribution of the dorsal and ventral hippocampus to learning in this task. Using photometry they observed activation of the dorsal and ventral hippocampus during sensory preconditioning and conditioning. Finally, the authors combined their sensory preconditioning task with DREADDs to examine the effect of inhibiting specific cell populations (CaMKII and PV) in the DH on the formation and retrieval/expression of mediated learning.

Strengths:

The authors provide one of the first demonstrations of auditory-visual sensory preconditioning in male mice. Research on the neurobiology of sensory preconditioning has primarily used rats as subjects. The development of a robust protocol in mice will be beneficial to the field, allowing researchers to take advantage of the many transgenic mouse lines. Indeed, in this study, the authors take advantage of a PV-Cre mouse line to examine the role of hippocampal PV cells in sensory preconditioning.

Weaknesses:

(1) The authors report that sensory preconditioning was observed in both male and female mice. However, their data only supports sensory preconditioning in male mice. In female mice, both paired and unpaired presentations of the light and tone in stage 1 led to increased freezing to the tone at test. In this case, fear to the tone could be attributed to factors other than sensory preconditioning, for example, generalization of fear between the auditory and visual stimulus.

(2) In the photometry experiment, the authors report an increase in neural activity in the hippocampus during both phase 1 (sensory preconditioning) and phase 2 (conditioning). In the subsequent experiment, they inhibit neural activity in the DH during phase 1 (sensory preconditioning) and the probe test, but do not include inhibition during phase 2 (conditioning). It was not clear why they didn't carry forward investigating the role of the hippocampus during phase 2 conditioning. Sensory preconditioning could occur due to the integration of the tone and shock during phase two, or retrieval and chaining of the tone-light-shock memories at test. These two possibilities cannot be differentiated based on the data. Given that we do not know at which stage the mediate learning is occurring, it would have been beneficial to additionally include inhibition of the DH during phase 2.

(3) In the final experiment, the authors report that inhibition of the dorsal hippocampus during the sensory preconditioning phase blocked mediated learning. While this may be the case, the failure to observe sensory preconditioning at test appears to be due more to an increase in baseline freezing (during the stimulus off period), rather than a decrease in freezing to the conditioned stimulus. Given the small effect, this study would benefit from an experiment validating that administration of J60 inhibited DH cells. Further, given that the authors did not observe any effect of DREADD inhibition in PV cells, it would also be important to validate successful cellular silencing in this protocol.

Reviewer #3 (Public review):

Summary:

Pinho et al. investigated the role of the dorsal vs ventral hippocampus and the gender differences in mediated learning. While previous studies already established the engagement of the hippocampus in sensory preconditioning, the authors here took advantage of freely-moving fiber photometry recording and chemogenetics to observe and manipulate sub-regions of the hippocampus (dorsal vs. ventral) in a cell-specific manner. The authors first found sex differences in the preconditioning phase of a sensory preconditioning procedure, where males required more preconditioning training than females for mediating learning to manifest, and where females displayed evidence of mediated learning even when neutral stimuli were never presented together within the session.

After validation of a sensory preconditioning procedure in mice using light and tone neutral stimuli and a mild foot shock as the unconditioned stimulus, the authors used fiber photometry to record from all neurons vs. parvalbumin_positive_only neurons in the dorsal hippocampus or ventral hippocampus of male mice during both preconditioning and conditioning phases. They found increased activity of all neurons, as well as PV+_only neurons in both sub-regions of the hippocampus during both preconditioning and conditioning phases. Finally, the authors found that chemogenetic inhibition of CaMKII+ neurons in the dorsal, but not ventral, hippocampus specifically prevented the formation of an association between the two neutral stimuli (i.e., light and tone cues), but not the direct association between the light cue and the mild foot shock. This set of data: (1) validates the mediated learning in mice using a sensory preconditioning protocol, and stresses the importance of taking sex effect into account; (2) validates the recruitment of dorsal and ventral hippocampi during preconditioning and conditioning phases; and (3) further establishes the specific role of CaMKII+ neurons in the dorsal but not ventral hippocampus in the formation of an association between two neutral stimuli, but not between a neutral-stimulus and a mild foot shock.

Strengths:

The authors developed a sensory preconditioning procedure in mice to investigate mediated learning using light and tone cues as neutral stimuli, and a mild foot shock as the unconditioned stimulus. They provide evidence of a sex effect in the formation of light-cue association. The authors took advantage of fiber-photometry and chemogenetics to target sub-regions of the hippocampus, in a cell-specific manner and investigate their role during different phases of a sensory conditioning procedure.

Weaknesses:

The authors went further than previous studies by investigating the role of sub-regions of the hippocampus in mediated learning, however, there are several weaknesses that should be noted:

(1) This work first validates mediated learning in a sensory preconditioning procedure using light and tone cues as neutral stimuli and a mild foot shock as the unconditioned stimulus, in both males and females. They found interesting sex differences at the behavioral level, but then only focused on male mice when recording and manipulating the hippocampus. The authors do not address sex differences at the neural level.

(2) As expected in fear conditioning, the range of inter-individual differences is quite high. Mice that didn't develop a strong light-->shock association, as evidenced by a lower percentage of freezing during the Probe Test Light phase, should manifest a low percentage of freezing during the Probe Test Tone phase. It would interesting to test for a correlation between the level of freezing during mediated vs test phases.

(3) The use of a synapsin promoter to transfect neurons in a non-specific manner does not bring much information. The authors applied a more specific approach to target PV+ neurons only, and it would have been more informative to keep with this cell-specific approach, for example by looking also at somatostatin+ inter-neurons.

(4) The authors observed event-related Ca2+ transients on hippocampal pan-neurons and PV+ inter-neurons using fiber photometry. They then used chemogenetics to inhibit CaMKII+ hippocampal neurons, which does not logically follow. It does not undermine the main finding of CaMKII+ neurons of the dorsal, but not ventral, hippocampus being involved in the preconditioning, but not conditioning, phase. However, observing CaMKII+ neurons (using fiber photometry) in mice running the same task would be more informative, as it would indicate when these neurons are recruited during different phases of sensory preconditioning. Applying then optogenetics to cancel the observed event-related transients (e.g., during the presentation of light and tone cues, or during the foot shock presentation) would be more appropriate.

(5) Probe tests always start with the "Probe Test Tone", followed by the "Probe Test Light". "Probe Test Tone" consists of an extinction session, which could affect the freezing response during "Probe Test Light" (e.g., Polack et al. (http://dx.doi.org/10.3758/s13420-013-0119-5)). Preferably, adding a group of mice with a Probe Test Light with no Probe Test Tone could help clarify this potential issue. The authors should at least discuss the possibility that the tone extinction session prior to the "Probe Test Light" could have affected the freezing response to the light cue.

Reviewer #4 (Public review):

Summary

Pinho et al use in vivo calcium imaging and chemogenetic approaches to examine the involvement of hippocampal sub-regions across the different stages of a sensory preconditioning task in mice. They find clear evidence for sensory preconditioning in male but not female mice. They also find that, in the male mice, CaMKII-positive neurons in the dorsal hippocampus: (1) encode the audio-visual association that forms in stage 1 of the task, and (2) retrieve/express sensory preconditioned fear to the auditory stimulus at test. These findings are supported by evidence that ranges from incomplete to convincing. They will be valuable to researchers in the field of learning and memory.

Abstract

Please note that sensory preconditioning doesn't require the stage 1 stimuli to be presented repeatedly or simultaneously.

"Finally, we combined our sensory preconditioning task with chemogenetic approaches to assess the role of these two hippocampal subregions in mediated learning."<br /> This implies some form of inhibition of hippocampal neurons in stage 2 of the protocol, as this is the only stage of the protocol that permits one to make statements about mediated learning. However, it is clear from what follows that the authors interrogate the involvement of hippocampal sub-regions in stages 1 and 3 of the protocol - not stage 2. As such, most statements about mediated learning throughout the paper are potentially misleading (see below for a further elaboration of this point). If the authors persist in using the term mediated learning to describe the response to a sensory preconditioned stimulus, they should clarify what they mean by mediated learning at some point in the introduction. Alternatively, they might consider using a different phrase such as "sensory preconditioned responding".

Introduction

"Low-salience" is used to describe stimuli such as tone, light, or odour that do not typically elicit responses that are of interest to experimenters. However, a tone, light, or odour can be very salient even though they don't elicit these particular responses. As such, it would be worth redescribing the "low-salience" stimuli in some other terms.

"These higher-order conditioning processes, also known as mediated learning, can be captured in laboratory settings through sensory preconditioning procedures2,6-11."<br /> Higher-order conditioning and mediated learning are not interchangeable terms: e.g., some forms of second-order conditioning are not due to mediated learning. More generally, the use of mediated learning is not necessary for the story that the authors develop in the paper and could be replaced for accuracy and clarity. E.g., "These higher-order conditioning processes can be studied in the laboratory using sensory preconditioning procedures2,6-11."

In reference to Experiment 2, it is stated that: "However, when light and tone were separated on time (Unpaired group), male mice were not able to exhibit mediated learning response (Figure 2B) whereas their response to the light (direct learning) was not affected (Figure 2D). On the other hand, female mice still present a lower but significant mediated learning response (Figure 2C) and normal direct learning (Figure 2E). Finally, in the No-Shock group, both male (Figure 2B and 2D) and female mice (Figure 2C and 2E) did not present either mediated or direct learning, which also confirmed that the exposure to the tone or light during Probe Tests do not elicit any behavioral change by themselves as the presence of the electric footshock is required to obtain a reliable mediated and direct learning responses."<br /> The absence of a difference between the paired and unpaired female mice should not be described as "significant mediated learning" in the latter. It should be taken to indicate that performance in the females is due to generalization between the tone and light. That is, there is no sensory preconditioning in the female mice. The description of performance in the No-shock group really shouldn't be in terms of mediated or direct learning: that is, this group is another control for assessing the presence of sensory preconditioning in the group of interest. As a control, there is no potential for them to exhibit sensory preconditioning, so their performance should not be described in a way that suggests this potential.

Methods - Behavior

I appreciate the reasons for testing the animals in a new context. This does, however, raise other issues that complicate the interpretation of any hippocampal engagement: e.g., exposure to a novel context may engage the hippocampus for exploration/encoding of its features - hence, it is engaged for retrieving/expressing sensory preconditioned fear to the tone. This should be noted somewhere in the paper given that one of its aims is to shed light on the broader functioning of the hippocampus in associative processes.

This general issue - that the conditions of testing were such as to force engagement of the hippocampus - is amplified by two further features of testing with the tone. The first is the presence of background noise in the training context and its absence in the test context. The second is the fact that the tone was presented for 30 s in stage 1 and then continuously for 180s at test. Both changes could have contributed to the engagement of the hippocampus as they introduce the potential for discrimination between the tone that was trained and tested.

Results - Behavior

The suggestion of sex differences based on differences in the parameters needed to generate sensory preconditioning is interesting. Perhaps it could be supported through some set of formal analyses. That is, the data in supplementary materials may well show that the parameters needed to generate sensory preconditioning in males and females are not the same. However, there needs to be some form of statistical comparison to support this point. As part of this comparison, it would be neat if the authors included body weight as a covariate to determine whether any interactions with sex are moderated by body weight.

What is the value of the data shown in Figure 1 given that there are no controls for unpaired presentations of the sound and light? In the absence of these controls, the experiment cannot have shown that "Female and male mice show mediated learning using an auditory-visual sensory preconditioning task" as implied by its title. Minimally, this experiment should be relabelled.

"Altogether, this data confirmed that we successfully set up an LTSPC protocol in mice and that this behavioral paradigm can be used to further study the brain circuits involved in higher-order conditioning."<br /> Please insert the qualifier that LTSPC was successfully established in male mice. There is no evidence of LTSPC in female mice.

Results - Brain

"Notably, the inhibition of CaMKII-positive neurons in the dHPC (i.e. J60 administration in DREADD-Gi mice) during preconditioning (Figure 4B), but not before the Probe Test 1 (Figure 4B), fully blocked mediated, but not direct learning (Figure 4D)."<br /> The right panel of Figure 4B indicates no difference between the controls and Group DPC in the percent change in freezing from OFF to ON periods of the tone. How does this fit with the claim that CaMKII-positive neurons in the dorsal hippocampus regulate associative formation during the session of tone-light exposures in stage 1 of sensory preconditioning?

Discussion

"When low salience stimuli were presented separated on time or when the electric footshock was absent, mediated and direct learning were abolished in male mice. In female mice, although light and tone were presented separately during the preconditioning phase, mediated learning was reduced but still present, which implies that female mice are still able to associate the two low-salience stimuli."<br /> This doesn't quite follow from the results. The failure of the female unpaired mice to withhold their freezing to the tone should not be taken to indicate the formation of a light-tone association across the very long interval that was interpolated between these stimulus presentations. It could and should be taken to indicate that, in female mice, freezing conditioned to the light simply generalized to the tone (i.e., these mice could not discriminate well between the tone and light).

"Indeed, our data suggests that when hippocampal activity is modulated by the specific manipulation of hippocampal subregions, this brain region is not involved during retrieval."<br /> Does this relate to the results that are shown in the right panel of Figure 4B, where there is no significant difference between the different groups? If so, how does it fit with the results shown in the left panel of this figure, where differences between the groups are observed?

"In line with this, the inhibition of CaMKII-positive neurons from the dorsal hippocampus, which has been shown to project to the restrosplenial cortex56, blocked the formation of mediated learning."<br /> Is this a reference to the findings shown in Figure 4B and, if so, which of the panels exactly? That is, one panel appears to support the claim made here while the other doesn't. In general, what should the reader make of data showing the percent change in freezing from stimulus OFF to stimulus ON periods?

Author response:

Reviewer #1 (Public review):

Summary:

The study by Pinho et al. presents a novel behavioral paradigm for investigating higher-order conditioning in mice. The authors developed a task that creates associations between light and tone sensory cues, driving mediated learning. They observed sex differences in task acquisition, with females demonstrating faster-mediated learning compared to males. Using fiber photometry and chemogenetic tools, the study reveals that the dorsal hippocampus (dHPC) plays a central role in encoding mediated learning. These findings are crucial for understanding how environmental cues, which are not directly linked to positive/negative outcomes, contribute to associative learning. Overall, the study is well-designed, with robust results, and the experimental approach aligns with the study's objectives.

Strengths:

(1) The authors develop a robust behavioral paradigm to examine higher-order associative learning in mice.

(2) They discover a sex-specific component influencing mediated learning, with females exhibiting enhanced learning abilities.

(3) Using fiber photometry and chemogenetic techniques, the authors identify the dorsal hippocampus but not the ventral hippocampus, which plays a crucial for encoding mediated learning.

Weaknesses:

(1) The study would be strengthened by further elaboration on the rationale for investigating specific cell types within the hippocampus.

We will add more information to better explain the rationale of our experiments and/or manipulations.

(2) The analysis of photometry data could be improved by distinguishing between early and late responses, as well as enhancing the overall presentation of the data.

We will provide new photometry analysis to differentiate between early and late responses during stimuli presentations.

(3) The manuscript would benefit from revisions to improve clarity and readability.

We will improve the clarity and readability of our manuscript.

Reviewer #2 (Public review):

Summary:

Pinho et al. developed a new auditory-visual sensory preconditioning procedure in mice and examined the contribution of the dorsal and ventral hippocampus to learning in this task. Using photometry they observed activation of the dorsal and ventral hippocampus during sensory preconditioning and conditioning. Finally, the authors combined their sensory preconditioning task with DREADDs to examine the effect of inhibiting specific cell populations (CaMKII and PV) in the DH on the formation and retrieval/expression of mediated learning.

Strengths:

The authors provide one of the first demonstrations of auditory-visual sensory preconditioning in male mice. Research on the neurobiology of sensory preconditioning has primarily used rats as subjects. The development of a robust protocol in mice will be beneficial to the field, allowing researchers to take advantage of the many transgenic mouse lines. Indeed, in this study, the authors take advantage of a PV-Cre mouse line to examine the role of hippocampal PV cells in sensory preconditioning.

Weaknesses:

(1) The authors report that sensory preconditioning was observed in both male and female mice. However, their data only supports sensory preconditioning in male mice. In female mice, both paired and unpaired presentations of the light and tone in stage 1 led to increased freezing to the tone at test. In this case, fear to the tone could be attributed to factors other than sensory preconditioning, for example, generalization of fear between the auditory and visual stimulus.

To address the pertinent doubt raised by the reviewer, we will perform new experiments to generate a new unpaired group in female mice through the increase of the temporal interval between light and tone exposure during the preconditioning phase. We believe this new results will bring additional information to better understand the performance of female mice in sensory preconditioning.

(2) In the photometry experiment, the authors report an increase in neural activity in the hippocampus during both phase 1 (sensory preconditioning) and phase 2 (conditioning). In the subsequent experiment, they inhibit neural activity in the DH during phase 1 (sensory preconditioning) and the probe test, but do not include inhibition during phase 2 (conditioning). It was not clear why they didn't carry forward investigating the role of the hippocampus during phase 2 conditioning. Sensory preconditioning could occur due to the integration of the tone and shock during phase two, or retrieval and chaining of the tone-light-shock memories at test. These two possibilities cannot be differentiated based on the data. Given that we do not know at which stage the mediate learning is occurring, it would have been beneficial to additionally include inhibition of the DH during phase 2.

We will perform new experiments to generate novel data by inhibiting the CamK-positive neurons of the dorsal hippocampus during the conditioning phase.

(3) In the final experiment, the authors report that inhibition of the dorsal hippocampus during the sensory preconditioning phase blocked mediated learning. While this may be the case, the failure to observe sensory preconditioning at test appears to be due more to an increase in baseline freezing (during the stimulus off period), rather than a decrease in freezing to the conditioned stimulus. Given the small effect, this study would benefit from an experiment validating that administration of J60 inhibited DH cells. Further, given that the authors did not observe any effect of DREADD inhibition in PV cells, it would also be important to validate successful cellular silencing in this protocol.

By combining chemogenetic and fiber photometry approaches, we will perform a control experiments to demonstrate that our chemogenetic experiments are decreasing CAMK- or PV-dependent activity in dorsal and ventral hippocampus.

Reviewer #3 (Public review):

Summary:

Pinho et al. investigated the role of the dorsal vs ventral hippocampus and the gender differences in mediated learning. While previous studies already established the engagement of the hippocampus in sensory preconditioning, the authors here took advantage of freely-moving fiber photometry recording and chemogenetics to observe and manipulate sub-regions of the hippocampus (dorsal vs. ventral) in a cell-specific manner. The authors first found sex differences in the preconditioning phase of a sensory preconditioning procedure, where males required more preconditioning training than females for mediating learning to manifest, and where females displayed evidence of mediated learning even when neutral stimuli were never presented together within the session.

After validation of a sensory preconditioning procedure in mice using light and tone neutral stimuli and a mild foot shock as the unconditioned stimulus, the authors used fiber photometry to record from all neurons vs. parvalbumin_positive_only neurons in the dorsal hippocampus or ventral hippocampus of male mice during both preconditioning and conditioning phases. They found increased activity of all neurons, as well as PV+_only neurons in both sub-regions of the hippocampus during both preconditioning and conditioning phases. Finally, the authors found that chemogenetic inhibition of CaMKII+ neurons in the dorsal, but not ventral, hippocampus specifically prevented the formation of an association between the two neutral stimuli (i.e., light and tone cues), but not the direct association between the light cue and the mild foot shock. This set of data: (1) validates the mediated learning in mice using a sensory preconditioning protocol, and stresses the importance of taking sex effect into account; (2) validates the recruitment of dorsal and ventral hippocampi during preconditioning and conditioning phases; and (3) further establishes the specific role of CaMKII+ neurons in the dorsal but not ventral hippocampus in the formation of an association between two neutral stimuli, but not between a neutral-stimulus and a mild foot shock.

Strengths:

The authors developed a sensory preconditioning procedure in mice to investigate mediated learning using light and tone cues as neutral stimuli, and a mild foot shock as the unconditioned stimulus. They provide evidence of a sex effect in the formation of light-cue association. The authors took advantage of fiber-photometry and chemogenetics to target sub-regions of the hippocampus, in a cell-specific manner and investigate their role during different phases of a sensory conditioning procedure.

Weaknesses:

The authors went further than previous studies by investigating the role of sub-regions of the hippocampus in mediated learning, however, there are several weaknesses that should be noted:

(1) This work first validates mediated learning in a sensory preconditioning procedure using light and tone cues as neutral stimuli and a mild foot shock as the unconditioned stimulus, in both males and females. They found interesting sex differences at the behavioral level, but then only focused on male mice when recording and manipulating the hippocampus. The authors do not address sex differences at the neural level.

As discussed above, we will perform additional experiment to evaluate the presence of a reliable sensory preconditioning in female mice. In addition, although observing sex differences at the neural level can be very interesting, we think that it is out of the scope of the present work. However, we will mention this issue/limitation in the Discussion in the new version of the manuscript.

(2) As expected in fear conditioning, the range of inter-individual differences is quite high. Mice that didn't develop a strong light-->shock association, as evidenced by a lower percentage of freezing during the Probe Test Light phase, should manifest a low percentage of freezing during the Probe Test Tone phase. It would interesting to test for a correlation between the level of freezing during mediated vs test phases.

We will provide correlations between the behavioral responses in both probe tests.

(3) The use of a synapsin promoter to transfect neurons in a non-specific manner does not bring much information. The authors applied a more specific approach to target PV+ neurons only, and it would have been more informative to keep with this cell-specific approach, for example by looking also at somatostatin+ inter-neurons.

We will better justify the use of specific promoters and the targeting of PV-positive neurons. We will also add discussion on potential interesting future experiments such as the targeting of other GABAergic subtypes.

(4) The authors observed event-related Ca2+ transients on hippocampal pan-neurons and PV+ inter-neurons using fiber photometry. They then used chemogenetics to inhibit CaMKII+ hippocampal neurons, which does not logically follow. It does not undermine the main finding of CaMKII+ neurons of the dorsal, but not ventral, hippocampus being involved in the preconditioning, but not conditioning, phase. However, observing CaMKII+ neurons (using fiber photometry) in mice running the same task would be more informative, as it would indicate when these neurons are recruited during different phases of sensory preconditioning. Applying then optogenetics to cancel the observed event-related transients (e.g., during the presentation of light and tone cues, or during the foot shock presentation) would be more appropriate.

We will perform new experiments to analyze the activity of CAMK-positive neurons during light-tone associations during the preconditioning phase in male mice.

(5) Probe tests always start with the "Probe Test Tone", followed by the "Probe Test Light". "Probe Test Tone" consists of an extinction session, which could affect the freezing response during "Probe Test Light" (e.g., Polack et al. (http://dx.doi.org/10.3758/s13420-013-0119-5)). Preferably, adding a group of mice with a Probe Test Light with no Probe Test Tone could help clarify this potential issue. The authors should at least discuss the possibility that the tone extinction session prior to the "Probe Test Light" could have affected the freezing response to the light cue.

We will add discussion on this issue raised by the reviewer.

Reviewer #4 (Public review):

Summary

Pinho et al use in vivo calcium imaging and chemogenetic approaches to examine the involvement of hippocampal sub-regions across the different stages of a sensory preconditioning task in mice. They find clear evidence for sensory preconditioning in male but not female mice. They also find that, in the male mice, CaMKII-positive neurons in the dorsal hippocampus: (1) encode the audio-visual association that forms in stage 1 of the task, and (2) retrieve/express sensory preconditioned fear to the auditory stimulus at test. These findings are supported by evidence that ranges from incomplete to convincing. They will be valuable to researchers in the field of learning and memory.

Abstract

Please note that sensory preconditioning doesn't require the stage 1 stimuli to be presented repeatedly or simultaneously.

We will correct this wrong sentence in the abstract.

"Finally, we combined our sensory preconditioning task with chemogenetic approaches to assess the role of these two hippocampal subregions in mediated learning."

This implies some form of inhibition of hippocampal neurons in stage 2 of the protocol, as this is the only stage of the protocol that permits one to make statements about mediated learning. However, it is clear from what follows that the authors interrogate the involvement of hippocampal sub-regions in stages 1 and 3 of the protocol - not stage 2. As such, most statements about mediated learning throughout the paper are potentially misleading (see below for a further elaboration of this point). If the authors persist in using the term mediated learning to describe the response to a sensory preconditioned stimulus, they should clarify what they mean by mediated learning at some point in the introduction. Alternatively, they might consider using a different phrase such as "sensory preconditioned responding".

Through the text, we will avoid the term “mediated learning” and we will replace it with more accurate terms. In addition, we will interrogate the role of dHPC in Stage 2 as commented above.

Introduction

"Low-salience" is used to describe stimuli such as tone, light, or odour that do not typically elicit responses that are of interest to experimenters. However, a tone, light, or odour can be very salient even though they don't elicit these particular responses. As such, it would be worth redescribing the "low-salience" stimuli in some other terms.

We will substitute “low-salience” for “innocuous”.

"These higher-order conditioning processes, also known as mediated learning, can be captured in laboratory settings through sensory preconditioning procedures2,6-11."

Higher-order conditioning and mediated learning are not interchangeable terms: e.g., some forms of second-order conditioning are not due to mediated learning. More generally, the use of mediated learning is not necessary for the story that the authors develop in the paper and could be replaced for accuracy and clarity. E.g., "These higher-order conditioning processes can be studied in the laboratory using sensory preconditioning procedures2,6-11."

Through the text, we will avoid the term “mediated learning” and we will replace it with more accurate terms.

In reference to Experiment 2, it is stated that: "However, when light and tone were separated on time (Unpaired group), male mice were not able to exhibit mediated learning response (Figure 2B) whereas their response to the light (direct learning) was not affected (Figure 2D). On the other hand, female mice still present a lower but significant mediated learning response (Figure 2C) and normal direct learning (Figure 2E). Finally, in the No-Shock group, both male (Figure 2B and 2D) and female mice (Figure 2C and 2E) did not present either mediated or direct learning, which also confirmed that the exposure to the tone or light during Probe Tests do not elicit any behavioral change by themselves as the presence of the electric footshock is required to obtain a reliable mediated and direct learning responses."<br /> The absence of a difference between the paired and unpaired female mice should not be described as "significant mediated learning" in the latter. It should be taken to indicate that performance in the females is due to generalization between the tone and light. That is, there is no sensory preconditioning in the female mice. The description of performance in the No-shock group really shouldn't be in terms of mediated or direct learning: that is, this group is another control for assessing the presence of sensory preconditioning in the group of interest. As a control, there is no potential for them to exhibit sensory preconditioning, so their performance should not be described in a way that suggests this potential.

We will re-write the text to clarify the right comments raised by the Reviewer.

Methods - Behavior

I appreciate the reasons for testing the animals in a new context. This does, however, raise other issues that complicate the interpretation of any hippocampal engagement: e.g., exposure to a novel context may engage the hippocampus for exploration/encoding of its features - hence, it is engaged for retrieving/expressing sensory preconditioned fear to the tone. This should be noted somewhere in the paper given that one of its aims is to shed light on the broader functioning of the hippocampus in associative processes.

We will further discuss this aspect on the manuscript.

This general issue - that the conditions of testing were such as to force engagement of the hippocampus - is amplified by two further features of testing with the tone. The first is the presence of background noise in the training context and its absence in the test context. The second is the fact that the tone was presented for 30 s in stage 1 and then continuously for 180s at test. Both changes could have contributed to the engagement of the hippocampus as they introduce the potential for discrimination between the tone that was trained and tested.

We will consider the aspect raised by the reviewer on the manuscript.

Results - Behavior

The suggestion of sex differences based on differences in the parameters needed to generate sensory preconditioning is interesting. Perhaps it could be supported through some set of formal analyses. That is, the data in supplementary materials may well show that the parameters needed to generate sensory preconditioning in males and females are not the same. However, there needs to be some form of statistical comparison to support this point. As part of this comparison, it would be neat if the authors included body weight as a covariate to determine whether any interactions with sex are moderated by body weight.

We will add statistical comparisons between male and female mice.

What is the value of the data shown in Figure 1 given that there are no controls for unpaired presentations of the sound and light? In the absence of these controls, the experiment cannot have shown that "Female and male mice show mediated learning using an auditory-visual sensory preconditioning task" as implied by its title. Minimally, this experiment should be relabelled.

We will relabel Figure 1.

"Altogether, this data confirmed that we successfully set up an LTSPC protocol in mice and that this behavioral paradigm can be used to further study the brain circuits involved in higher-order conditioning."

Please insert the qualifier that LTSPC was successfully established in male mice. There is no evidence of LTSPC in female mice.

We will generate new experiments to try to demonstrate that SPC can be also observed in female mice.

Results - Brain

"Notably, the inhibition of CaMKII-positive neurons in the dHPC (i.e. J60 administration in DREADD-Gi mice) during preconditioning (Figure 4B), but not before the Probe Test 1 (Figure 4B), fully blocked mediated, but not direct learning (Figure 4D)."

The right panel of Figure 4B indicates no difference between the controls and Group DPC in the percent change in freezing from OFF to ON periods of the tone. How does this fit with the claim that CaMKII-positive neurons in the dorsal hippocampus regulate associative formation during the session of tone-light exposures in stage 1 of sensory preconditioning?

We will rephrase and add more Discussion regarding this section of the results to stick to what the graphs are showing. We will clarify that the group where dHPC activity is inhibited during preconditioning is the only one where the % of change is not significantly different from 0 (compared to the control or the group where the dHPC activity was modulated during the test).

Discussion

"When low salience stimuli were presented separated on time or when the electric footshock was absent, mediated and direct learning were abolished in male mice. In female mice, although light and tone were presented separately during the preconditioning phase, mediated learning was reduced but still present, which implies that female mice are still able to associate the two low-salience stimuli."

This doesn't quite follow from the results. The failure of the female unpaired mice to withhold their freezing to the tone should not be taken to indicate the formation of a light-tone association across the very long interval that was interpolated between these stimulus presentations. It could and should be taken to indicate that, in female mice, freezing conditioned to the light simply generalized to the tone (i.e., these mice could not discriminate well between the tone and light).

We will rewrite this part depending on the results observed in female mice.

"Indeed, our data suggests that when hippocampal activity is modulated by the specific manipulation of hippocampal subregions, this brain region is not involved during retrieval."

Does this relate to the results that are shown in the right panel of Figure 4B, where there is no significant difference between the different groups? If so, how does it fit with the results shown in the left panel of this figure, where differences between the groups are observed?

We will re-write it to clearly describe our results and we will also revise all the statistical analysis.

"In line with this, the inhibition of CaMKII-positive neurons from the dorsal hippocampus, which has been shown to project to the restrosplenial cortex56, blocked the formation of mediated learning."

Is this a reference to the findings shown in Figure 4B and, if so, which of the panels exactly? That is, one panel appears to support the claim made here while the other doesn't. In general, what should the reader make of data showing the percent change in freezing from stimulus OFF to stimulus ON periods?

We will rewrite the text to clearly describe our results, and we will also revise all the statistical analysis. In addition, we will better explain the data showing the % of change.

eLife Assessment

In this paper, the authors report important structural and functional findings on the interaction of how the group A streptococci (GAS) M3 protein (expressed on GAS strains emm3, which are associated with invasive disease) binds to human collagens. They demonstrate an unusual T-shaped structure within the N-terminal hypervariable region of M3 protein that can bind two copies of collagen triple helix in parallel. These solid data advance understanding of how GAS M3 interacts with human collagen, information relevant to understanding and developing treatments for GAS infection. A major limitation of the work is the lack of mutational work to test if the T-shaped structure is necessary for binding collagen.

Reviewer #1 (Public review):

Summary:

Wojnowska et al. report structural and functional studies of the interaction of Streptococcus pyogenes M3 protein with collagen. They show through X-ray crystallographic studies that the N-terminal hypervariable region of M3 protein forms a T-like structure and that the T-like structure binds a three-stranded collagen-mimetic peptide. They indicate that the T-like structure is predicted by AlphaFold3 (with varying confidence level) in other M proteins that have sequence similarity to M3 protein and M-like proteins from group C and G streptococci. For some, but not all, of these related M and M-like proteins, AlphaFold3 predicts complexes similar to the one observed for M3-collagen. Functionally, the authors show that emm3 strains form biofilms with more mass when surfaces are coated with collagen, and this effect can be blocked by an M3 protein fragment that contains the T-structure. They also show the co-occurrence of emm3 strains and collagen in patient biopsies and a skin tissue organoid.

Strengths:

The paper is well-written and the data presented is mostly sound.

Weaknesses:

However, a major limitation of the paper is that it is almost entirely observational and fails to draw a causal relationship. This is mainly due to the near-total absence of mutational studies.

Reviewer #2 (Public review):

Streptococcus pyogenes, or group A streptococci (GAS) can cause diseases ranging from skin and mucosal infections, to plasma invasion, and post-infection autoimmune syndromes. M proteins are essential GAS virulence factors that include an N-terminal hypervariable region (HVR). M proteins are known to bind to numerous human proteins; a small subset of M proteins were reported to bind collagen, which is thought to promote tissue adherence. In this paper, the authors characterize M3 interactions with collagen and its role in biofilm formation. Specifically, they screened different collagen type II and III variants for full-length M3 protein binding using an ELISA-like method, detecting anti-GST antibody signal. By statistical analysis, hydrophobic amino acids and hydroxyproline were found to positively support binding, whereas acidic residues and proline negatively impacted binding (Table 1). The authors applied X-ray crystallography to determine the structure of the N-terminal domain (42-151 amino acids) of M3 protein (M3-NTD). M3-NTD dimmer (PDB 8P6K) forms a T-shaped structure with three helices (H1, H2, H3), which are stabilized by a hydrophobic core, inter-chain salt bridges and hydrogen bonds on H1, H2 helices, and H3 coiled coil. The conserved Gly113 serves as the turning point between H2 and H3 (Figure 5). The M3-NTD is co-crystalized with a 24-residue peptide, JDM238, to determine the structure of M3-collagen binding. The structure (PDB 8P6J) shows that two copies of collagen in parallel bind to H1 and H2 of M3-NTD. Among the residues involved in binding, conserved Try96 is shown to play a critical role supported by structure and isothermal titration calorimetry (ITC). The authors also apply a crystal-violet assay and fluorescence microscopy to determine that M3 is involved in collagen type I binding, but not M1 or M28 (Figure 9). Tissue biopsy staining indicates that M3 strains co-localize with collagen IV-containing tissue, while M1 strains do not. The authors provide generally compelling evidence to show that GAS M3 protein binds to collagen, and plays a critical role in forming biofilms, which contribute to disease pathology. This is a very well-executed study and a well-written report relevant to understanding GAS pathogenesis and approaches to combatting disease; data are also applicable to emerging human pathogen Streptococcus dysgalactiae. One caveat that was not entirely resolved is if/how different collagen types might impact M3 binding and function. Due to the technical constraints, the in vitro structure and other binding assays use type II collagen whereas in vivo, biofilm formation assays and tissue biopsy staining use type I and IV collagen; it was unclear if this difference is significant. One possibility is that M3 has an unbiased binding to all types of collagens, only the distribution of collagens leads to the finding that M3 binds to type IV (basement membrane) and type I (varies of tissue including skin), rather than type II (cartilage).

Author response:

Many thanks for assessing our submission. We are grateful for the reviews and recommendations that will inform a revised version of the paper, which will include additional data and modified text to take into account the reviewers’ comments.

We appreciate Reviewer #1’s suggestion regarding the use of mutational work to demonstrate that collagen binding is indeed dependent on the T-shaped fold. However, we believe that this approach is neither feasible nor necessary for our study. Instead, we propose to measure collagen binding to a monomeric form of M3, which preserves all residues including the ones involved in binding, but cannot form the T-shaped structure. This will achieve the same as unravelling the T fold through mutations, but at the same time removes the risk of directly affecting binding through altering residues that are involved in both binding and definition of the T fold.

Structural biology is by its nature observational, which is not a limitation but the very purpose of this approach. Our study goes beyond observing structures. We identify a critical residue within a previously mapped binding site, and demonstrate through mutagenesis a causal link between presence of this residue on a tertiary fold and collagen binding activity. We will firm up our mutational experiments with a characterisation of the M3 Tyr96 variants to confirm that these mutations did not affect the overall fold. We further demonstrate that the interaction between M3 and collagen promotes biofilm formation as observed in patient biopsies and a tissue model of infection. We show that other streptococci, that do not possess a surface protein presenting collagen binding sites like M3, do not form collagen-dependent biofilm. We therefore do not think that criticising our study for being almost entirely observational is justified. 

We thank Reviewer #2 for the thorough analysis of our reported findings. The main criticism here concerns the question if binding of emm3 streptococci would differ for different types of collagen. We will address this point in the revised manuscript. Our collagen peptide binding assays together with the structural data identify the collagen triple helix as the binding site for M3. While collagen types differ in their functions and morphology in various tissues, they all have in common triple-helical tropocollagen regions (with very high sequence similarity) that are non-specifically recognised by M3. Therefore, our data in conjunction with the body of published work showing binding of M3 to collagens I, II, III and IV suggest it is highly likely that emm3 streptococci will indeed bind to many if not all types of collagen in the same manner. Whether this means all collagen types, in the various tissues where they occur, are targeted by emm3 streptococci is a very interesting question, however one that goes beyond the scope of our study.

eLife Assessment

This important theoretical study introduces an extension to the commonly used SIR model for infectious disease dynamics, to explicitly consider the role of larger group sizes. Instead of the commonly used individual-based network models, the authors developed a simplified approach based on group sampling, with discrete high- and low-risk groups, which makes the results easier to produce and interpret, at the cost of less detail in the model. The evidence is convincing in terms of the soundness of the theoretical projections and the impact that accounting for group sizes may have on inferences from surveillance data. However, it has not yet been demonstrated that the predictions provide more realistic projections when based on real-world data.

Reviewer #1 (Public review):

Summary:

This work considers the biases introduced into pathogen surveillance due to congregation effects, and also models homophily and variants/clades. The results are primarily quantitative assessments of this bias but some qualitative insights are gained e.g. that initial variant transmission tends to be biased upwards due to this effect, which is closely related to classical founder effects.

Strengths:

The model considered involves a simplification of the process of congregation using multinomial sampling that allows for a simpler and more easily interpretable analysis.

Weaknesses:

This simplification removes some realism, for example, detailed temporal transmission dynamics of congregations.

Reviewer #2 (Public review):

Summary:

In "Founder effects arising from gathering dynamics systematically bias emerging pathogen surveillance" Bradford and Hang present an extension to the SIR model to account for the role of larger than pairwise interactions in infectious disease dynamics. They explore the impact of accounting for group interactions on the progression of infection through the various sub-populations that make up the population as a whole. Further, they explore the extent to which interaction heterogeneity can bias epidemiological inference from surveillance data in the form of IFR and variant growth rate dynamics. This work advances the theoretical formulation of the SIR model and may allow for more realistic modeling of infectious disease outbreaks in the future.

Strengths:

(1) This work addresses an important limitation of standard SIR models. While this limitation has been addressed previously in the form of network-based models, those are, as the authors argue, difficult to parameterize to real-world scenarios. Further, this work highlights critical biases that may appear in real-world epidemiological surveillance data. Particularly, over-estimation of variant growth rates shortly after emergence has led to a number of "false alarms" about new variants over the past five years (although also to some true alarms).

(2) While the results presented here generally confirm my intuitions on this topic, I think it is really useful for the field to have it presented in such a clear manner with a corresponding mathematical framework. This will be a helpful piece of work to point to to temper concerns about rapid increases in the frequency of rare variants.

(3) The authors provide a succinct derivation of their model that helps the reader understand how they arrived at their formulation starting from the standard SIR model.

(4) The visualizations throughout are generally easy to interpret and communicate the key points of the authors' work.

(5) I thank the authors for providing detailed code to reproduce manuscript figures in the associated GitHub repo.

Weaknesses:

(1) The authors argue that network-based SIR models are difficult to parameterize (line 66), however, the model presented here also has a key parameter, mainly P_n, or the distribution of risk groups in the population. I think it is important to explore the extent to which this parameter can be inferred from real-world data to assess whether this model is, in practice, any easier to parameterize.

(2) The authors explore only up to four different risk groups, accounting for only four-wise interactions. But, clearly, in real-world settings, there can be much larger gatherings that promote transmission. What was the justification for setting such a low limit on the maximum group size? I presume it's due to computational efficiency, which is understandable, but it should be discussed as a limitation.

(3) Another key limitation that isn't addressed by the authors is that there may be population structure beyond just risk heterogeneity. For example, there may be two separate (or, weakly connected) high-risk sub-groups. This will introduce temporal correlation in interactions that are not (and can not easily be) captured in this model. My instinct is that this would dampen the difference between risk groups shown in Figure 2A. While I appreciate the authors's desire to keep their model relatively simple, I think this limitation should be explicitly discussed as it is, in my opinion, relatively significant.

Author response:

Reviewer #1 (Public review):

Summary:

This work considers the biases introduced into pathogen surveillance due to congregation effects, and also models homophily and variants/clades. The results are primarily quantitative assessments of this bias but some qualitative insights are gained e.g. that initial variant transmission tends to be biased upwards due to this effect, which is closely related to classical founder effects.

Strengths:

The model considered involves a simplification of the process of congregation using multinomial sampling that allows for a simpler and more easily interpretable analysis.

Weaknesses:

This simplification removes some realism, for example, detailed temporal transmission dynamics of congregations.

We appreciate Reviewer #1's comments. We hope our framework, like the classic SIR model, can be adapted in the future to build more complex and realistic models.

Reviewer #2 (Public review):

Summary:

In "Founder effects arising from gathering dynamics systematically bias emerging pathogen surveillance" Bradford and Hang present an extension to the SIR model to account for the role of larger than pairwise interactions in infectious disease dynamics. They explore the impact of accounting for group interactions on the progression of infection through the various sub-populations that make up the population as a whole. Further, they explore the extent to which interaction heterogeneity can bias epidemiological inference from surveillance data in the form of IFR and variant growth rate dynamics. This work advances the theoretical formulation of the SIR model and may allow for more realistic modeling of infectious disease outbreaks in the future.

Strengths:

(1) This work addresses an important limitation of standard SIR models. While this limitation has been addressed previously in the form of network-based models, those are, as the authors argue, difficult to parameterize to real-world scenarios. Further, this work highlights critical biases that may appear in real-world epidemiological surveillance data. Particularly, over-estimation of variant growth rates shortly after emergence has led to a number of "false alarms" about new variants over the past five years (although also to some true alarms).

(2) While the results presented here generally confirm my intuitions on this topic, I think it is really useful for the field to have it presented in such a clear manner with a corresponding mathematical framework. This will be a helpful piece of work to point to to temper concerns about rapid increases in the frequency of rare variants.

(3) The authors provide a succinct derivation of their model that helps the reader understand how they arrived at their formulation starting from the standard SIR model.

(4) The visualizations throughout are generally easy to interpret and communicate the key points of the authors' work.

(5) I thank the authors for providing detailed code to reproduce manuscript figures in the associated GitHub repo.

Weaknesses:

(1) The authors argue that network-based SIR models are difficult to parameterize (line 66), however, the model presented here also has a key parameter, mainly P_n, or the distribution of risk groups in the population. I think it is important to explore the extent to which this parameter can be inferred from real-world data to assess whether this model is, in practice, any easier to parameterize.

(2) The authors explore only up to four different risk groups, accounting for only four-wise interactions. But, clearly, in real-world settings, there can be much larger gatherings that promote transmission. What was the justification for setting such a low limit on the maximum group size? I presume it's due to computational efficiency, which is understandable, but it should be discussed as a limitation.

(3) Another key limitation that isn't addressed by the authors is that there may be population structure beyond just risk heterogeneity. For example, there may be two separate (or, weakly connected) high-risk sub-groups. This will introduce temporal correlation in interactions that are not (and can not easily be) captured in this model. My instinct is that this would dampen the difference between risk groups shown in Figure 2A. While I appreciate the authors's desire to keep their model relatively simple, I think this limitation should be explicitly discussed as it is, in my opinion, relatively significant.

We appreciate Reviewer 2's thoughtful comments and wish to address some of the weaknesses:

We agree that inferring P_n from real data will be challenging, but think this is an important direction for future research. Further, we’d like to reframe our claim that our approach is "easier to parameterize" than network models. Rather, P_n has fewer degrees of freedom than analogous network models, just as many different networks can share the same degree distribution. Fewer degrees of freedom mean that we expect our model to suffer from fewer identifiability issues when fitting to data, though non-identifiability is often inescapable in models of this nature (e.g., \beta and \gamma in the SIR model are not uniquely identifiable during exponential growth). Whether this is more or less accurate is another question. Classic bias-variance tradeoffs argue that a model with a moderate complexity trained on one data set can better fit future data than overly simple or overly complex models.

We chose four risk groups for purposes of illustration, but this can be increased arbitrarily. It should be noted that the simulation bottleneck when increasing the numbers of risk groups is numerical due the stiffness of the ODEs. This arises because the nonlinearity of infection terms scales with the number of risk groups (e.g., ~ \beta * S * I^3 for 4 risk groups). As such, a careful choice of numerical solvers may be required when integrating the ODEs. Meanwhile, this is not an issue for stochastic, individual based implementation (e.g., Gillespie). As for how well this captures super-spreading, we believe choosing smaller risk groups does not hinder modeling disease spread at large gatherings. Consider a statistical interpretation, where individuals at a large gathering engage in a series of smaller interactions over time (e.g., 2/3/4/etc person conversations). The key determinants of the resulting gathering size distribution at any one large gathering are the number of individuals within some shared proximity over time and the infectiousness/dispersal of the pathogen. Of course, whether this interpretation is a sufficient approximation for classic super-spreading events (e.g., funerals during 2014-2015 West Africa Ebola outbreak) is a matter of debate. Our framework is best interpreted at a population level where the effects of any single gathering are washed out by the overall gathering distribution, P_n. As the prior weakness highlighted, establishing P_n is challenging, but we believe empirically measuring proxies of it may provide future insight in how behavior impacts disease spread. For example, prior work has combined contact tracing and co-location data from connection to WiFi networks to estimate the distribution of contacts per individual, and its degree of overdispersion (Petros et al. Med 2022).

We chose to introduce our framework in a simple SIR context familiar to many readers. This decision does not in any way limit applying it to settings with more population structure. Rather, we believe our framework is easily adaptable and that our presentation (hopefully) makes it clear how to do this. For example, two weakly connected groups could be easily achieved by (for each gathering) first sampling the preferred group and then sampling from the population in a biased manner. The biased sampling could even be a function of gathering sizes, time, etc. The resulting infection terms are still (sums of) multinomials. More generally, the sampling probabilities for an individual of some type need not be its frequency (e.g., S/N, I/N). Indeed, we believe generating models with complex social interactions is both simplified and made more robust by focusing on modeling the generative process of attending gatherings.

eLife Assessment

The study introduces new tools for measuring the intracellular calcium concentration close to transmitter release sites, which may be relevant for synaptic vesicle fusion and replenishment. This approach yields important new information about the spatial and temporal profile of calcium concentrations near the site of entry at the plasma membrane. This experimental work is complemented by a coherent, open-source, computational model that successfully describes changes in calcium domains. Key gaps in the data presented mean that the evidence for the main conclusions is currently incomplete.

Reviewer #1 (Public review):

This paper describes technically-impressive measurements of calcium signals near synaptic ribbons in goldfish bipolar cells. The data presented provides high spatial and temporal resolution information about calcium concentrations along the ribbon at various distances from the site of entry at the plasma membrane. This is important information. Important gaps in the data presented mean that the evidence for the main conclusions is currently inadequate.

Strengths

(1) The technical aspects of the measurements are impressive. The authors use calcium indicators bound to the ribbon and high-speed line scans to resolve changes with a spatial resolution of ~250 nm and a temporal resolution of less than 10 ms. These spatial and temporal scales are much closer to those relevant for vesicle release than previous measurements.

(2) The use of calcium indicators with very different affinities and different intracellular calcium buffers helps provide confirmation of key results.

Weaknesses

(1) Multiple key points of the paper lack statistical tests or summary data from populations of cells. For example, the text states that the proximal and distal calcium kinetics in Figure 2A differ. This is not clear from the inset to Figure 2A - where the traces look like scaled versions of each other. Values for time to half-maximal peak fluorescence are given for one example cell but no statistics or summary are provided. Figure 8 shows examples from one cell with no summary data. This issue comes up in other places as well.

(2) Figure 5 is confusing. The figure caption describes red, green, and blue traces, but the figure itself has only two traces in each panel and none are red, green, or blue. It's not possible currently to evaluate this figure.

(3) The rise time measurements in Figure 2 are very different for low and high-affinity indicators, but no explanation is given for this difference. Similarly, the measurements of peak calcium concentration in Figure 4 are very different from the two indicators. That might suggest that the high-affinity indicator is strongly saturated, which raises concerns about whether that is impacting the kinetic measurements.

Reviewer #2 (Public review):

Summary:

The study introduces new tools for measuring intracellular Ca2+ concentration gradients around retinal rod bipolar cell (rbc) synaptic ribbons. This is done by comparing the Ca2+ profiles measured with mobile Ca2+ indicator dyes versus ribbon-tethered (immobile) Ca2+ indicator dyes. The Ca2+ imaging results provide a straightforward demonstration of Ca2+ gradients around the ribbon and validate their experimental strategy. This experimental work is complemented by a coherent, open-source, computational model that successfully describes changes in Ca2+ domains as a function of Ca2+ buffering. In addition, the authors try to demonstrate that there is heterogeneity among synaptic ribbons within an individual rbc terminal.

Strengths:

The study introduces a new set of tools for estimating Ca2+ concentration gradients at ribbon AZs, and the experimental results are accompanied by an open-source, computational model that nicely describes Ca2+ buffering at the rbc synaptic ribbon. In addition, the dissociated retinal preparation remains a valuable approach for studying ribbon synapses. Lastly, excellent EM.

Weaknesses:

Heterogeneity in the spatiotemporal dynamics of Ca2+ influx was not convincingly related to ribbon size, nor was the functional relevance of Ca2+ dynamics to rod bipolars demonstrated (e.g., exocytosis to different postsynaptic targets). In addition, the study would benefit from the inclusion of the Ca2+ currents that were recorded in parallel with the Ca2+ imaging.

Reviewer #3 (Public review):

Summary:

In this study, the authors have developed a new Ca indicator conjugated to the peptide, which likely recognizes synaptic ribbons, and have measured microdomain Ca near synaptic ribbons at retinal bipolar cells. This interesting approach allows one to measure Ca close to transmitter release sites, which may be relevant for synaptic vesicle fusion and replenishment. Though microdomain Ca at the active zone of ribbon synapses has been measured by Hudspeth and Moser, the new study uses the peptide recognizing synaptic ribbons, potentially measuring the Ca concentration relatively proximal to the release sites.

Strengths:

The study is in principle technically well done, and the peptide approach is technically interesting, which allows one to image Ca near the particular protein complexes. The approach is potentially applicable to other types of imaging.

Weaknesses:

Peptides may not be entirely specific, and the genetic approach tagging particular active zone proteins with fluorescent Ca indicator proteins may well be more specific. I also feel that "Nano-physiology" is overselling, because the measured Ca is most likely the local average surrounding synaptic ribbons. With this approach, nobody knows about the real release site Ca or the Ca relevant for synaptic vesicle replenishment. It is rather "microdomain physiology" which measures the local Ca near synaptic ribbons, relatively large structures responsible for fusion, replenishment, and recycling of synaptic vesicles.

Author response:

Public Reviews:

Reviewer #1 (Public review):

This paper describes technically-impressive measurements of calcium signals near synaptic ribbons in goldfish bipolar cells. The data presented provides high spatial and temporal resolution information about calcium concentrations along the ribbon at various distances from the site of entry at the plasma membrane. This is important information. Important gaps in the data presented mean that the evidence for the main conclusions is currently inadequate.

Strengths

(1) The technical aspects of the measurements are impressive. The authors use calcium indicators bound to the ribbon and high-speed line scans to resolve changes with a spatial resolution of ~250 nm and a temporal resolution of less than 10 ms. These spatial and temporal scales are much closer to those relevant for vesicle release than previous measurements.

(2) The use of calcium indicators with very different affinities and different intracellular calcium buffers helps provide confirmation of key results.

Thank you very much for this positive evaluation of our work.

Weaknesses

(1) Multiple key points of the paper lack statistical tests or summary data from populations of cells. For example, the text states that the proximal and distal calcium kinetics in Figure 2A differ. This is not clear from the inset to Figure 2A - where the traces look like scaled versions of each other. Values for time to half-maximal peak fluorescence are given for one example cell but no statistics or summary are provided. Figure 8 shows examples from one cell with no summary data. This issue comes up in other places as well.

Thank you for this feedback. We will address this in our revised manuscript.

(2) Figure 5 is confusing. The figure caption describes red, green, and blue traces, but the figure itself has only two traces in each panel and none are red, green, or blue. It's not possible currently to evaluate this figure.

Thank you for pointing out this oversight. The figure indeed only shows the proximal and distal calcium signals, but not the cytoplasmic ones. The figure will be corrected in our revised manuscript.

(3) The rise time measurements in Figure 2 are very different for low and high-affinity indicators, but no explanation is given for this difference. Similarly, the measurements of peak calcium concentration in Figure 4 are very different from the two indicators. That might suggest that the high-affinity indicator is strongly saturated, which raises concerns about whether that is impacting the kinetic measurements.

As we had mentioned in the text, we do believe that the high-affinity version is partially saturated. This will be a problem for strong depolarizations and signals near the membrane. The higher affinity indicators are more useful for reporting calcium levels on the ribbon after the depolarization when the signal from the low affinity indicators is small. We will address this in the discussion of the revision.

Reviewer #2 (Public review):

Summary:

The study introduces new tools for measuring intracellular Ca2+ concentration gradients around retinal rod bipolar cell (rbc) synaptic ribbons. This is done by comparing the Ca2+ profiles measured with mobile Ca2+ indicator dyes versus ribbon-tethered (immobile) Ca2+ indicator dyes. The Ca2+ imaging results provide a straightforward demonstration of Ca2+ gradients around the ribbon and validate their experimental strategy. This experimental work is complemented by a coherent, open-source, computational model that successfully describes changes in Ca2+ domains as a function of Ca2+ buffering. In addition, the authors try to demonstrate that there is heterogeneity among synaptic ribbons within an individual rbc terminal.

Strengths:

The study introduces a new set of tools for estimating Ca2+ concentration gradients at ribbon AZs, and the experimental results are accompanied by an open-source, computational model that nicely describes Ca2+ buffering at the rbc synaptic ribbon. In addition, the dissociated retinal preparation remains a valuable approach for studying ribbon synapses. Lastly, excellent EM.

Thank you very much for this appreciation.

Weaknesses:

Heterogeneity in the spatiotemporal dynamics of Ca2+ influx was not convincingly related to ribbon size, nor was the functional relevance of Ca2+ dynamics to rod bipolars demonstrated (e.g., exocytosis to different postsynaptic targets). In addition, the study would benefit from the inclusion of the Ca2+ currents that were recorded in parallel with the Ca2+ imaging.

Thank you for this critique. We agree that the relationship between size and Ca2+ signal is not established by our recordings. By analogy to the hair cell literature, we believe that it is a reasonable hypothesis, but more studies will be necessary to definitively determine whether the signal relates to the ribbon size or synaptic signaling. This will be addressed in future experiments.

We will include the Ca²⁺ currents in the revision.

Reviewer #3 (Public review):

Summary:

In this study, the authors have developed a new Ca indicator conjugated to the peptide, which likely recognizes synaptic ribbons, and have measured microdomain Ca near synaptic ribbons at retinal bipolar cells. This interesting approach allows one to measure Ca close to transmitter release sites, which may be relevant for synaptic vesicle fusion and replenishment. Though microdomain Ca at the active zone of ribbon synapses has been measured by Hudspeth and Moser, the new study uses the peptide recognizing synaptic ribbons, potentially measuring the Ca concentration relatively proximal to the release sites.

Strengths:

The study is in principle technically well done, and the peptide approach is technically interesting, which allows one to image Ca near the particular protein complexes. The approach is potentially applicable to other types of imaging.

Thank you very much for this appreciation.

Weaknesses:

Peptides may not be entirely specific, and the genetic approach tagging particular active zone proteins with fluorescent Ca indicator proteins may well be more specific. I also feel that "Nano-physiology" is overselling, because the measured Ca is most likely the local average surrounding synaptic ribbons. With this approach, nobody knows about the real release site Ca or the Ca relevant for synaptic vesicle replenishment. It is rather "microdomain physiology" which measures the local Ca near synaptic ribbons, relatively large structures responsible for fusion, replenishment, and recycling of synaptic vesicles.

The peptide approach has been used fairly extensively in the ribbon synapse field and the evidence that it efficiently labels the ribbon is well established, however, we do acknowledge that the peptide is in equilibrium with a cytoplasmic pool. Thus, some of the signal arises from this cytoplasmic pool. The alternative of a genetically encoded Ca-indicator concatenated to a ribbon protein would not have this problem, but would be more limited in flexibility in changing calcium indicators. We believe both approaches have their merits, each with separate advantages and disadvantages.

As for the nano vs. micro argument, we certainly do not want to suggest that we are measuring the same nano-domains, in the 10s of nanometers, that drive neurotransmitter release, but we do believe we are in the sub-micrometer--100s of nm—range. We chose the term based on the usage by other authors to describe similar measurements (Neef et al., 2018; https://doi.org/10.1038/s41467-017-02612-y), but we see the reviewer’s point. To avoid confusion, we will change the title in the revision.

eLife Assessment

This study presents valuable findings on the increased prevalence of pain in women with polycystic ovary syndrome and its relationship to health outcomes. The evidence supporting the conclusions is compelling with a large number of patients and sound methodology, and can be used as a starting point for studies of etiology and mechanisms of pain in women with polycystic ovary syndrome and comorbidities. The work will be of interest to medical biologists working on polycystic ovary syndrome pathophysiology and clinicians.

Reviewer #1 (Public review):

Summary:

This retrospective study provides new data regarding the prevalence of pain in women with PCOS and its relationship with health outcomes. Using data from electronic health records (EHR), the authors found a significantly higher prevalence of pain among women with PCOS compared to those without the condition: 19.21% of women with PCOS versus 15.8% in non-PCOS women. The highest prevalence of pain was conducted among Black or African American (32.11%) and White (30.75%) populations. Besides, women with PCOS and pain have at least a 2-fold increased prevalence of obesity (34.68%) at baseline compared to women with PCOS in general (16.11%). Also, women with PCOS had the highest risk for infertility and T2D, but women with PCOS and pain had higher risks for ovarian cysts and liver disease. Regarding these results, the authors suggested the critical need to address pain in the diagnosis and management of PCOS due to its significant impact on patient health outcomes.

Strengths:

(1) The problem of pain assessment in PCOS patients is well described and the authors provided a clear rationale selection of the retrospective design to investigate this problem.

(2) A large number of analyzed patient records (76,859,666 women) and their uniformity increases the power of the study. Using the Propensity Score Matching makes it possible to reduce the heterogeneity of the compared cohorts and the influence of comorbid conditions.

(3) Analysis in different ethnic cohorts provides actual and necessary data regarding the prevalence of pain and its relationship with different health conditions that will be helpful for clinicians to make a diagnosis and manage PCOS in women of different ethnicities.

(4) Assessment of the risk of different health conditions including PCOS-associated pathology as other common groups of diseases in PCOS women with or without pain allows to differentiate the risk of comorbid conditions depending on the presence of one symptom (pelvic or abdominal pain, dysmenorrhea).

Weaknesses:

(1) Although the paper has strengths in methodology and data analysis, it also has some weaknesses. The lack of a hypothesis doesn't allow us to evaluate the aim and significance of this study.

(2) The exclusion criteria don't include conditions, that can lead to symptoms similar to PCOS: thyroid diseases, hyperprolactinemia, and congenital adrenal hyperplasia. Thyroid status is not being taken into account in the criteria for matching. All these conditions could occur as on prevalence results as on risk assessment.

(3) The significant weakness of the study is the absence of a Latin American cohort. Probably the White cohort includes Latin Americans or others, but the results of the study cannot be extrapolated to particular White ethnicities.

(4) The authors didn't provide sufficient rationale for future health outcomes and this list didn't include diseases of the digestive system or disorders of thyroid glands, which can also cause abdominal pain.

Reviewer #2 (Public review):

Summary:

The study offers a thorough analysis of the prevalence of pain in women with polycystic ovary syndrome (PCOS) and its associations with health outcomes across various racial groups. Furthermore, the research investigates the prevalence of PCOS and pain among different racial demographics, as well as the increased risk of developing various conditions in comparison to individuals who have PCOS alone.

Strengths:

The study emphasizes pain as a significant comorbidity of PCOS, an area that is critically underexplored in existing literature. The findings regarding the increased prevalence of some of the diseases in the PCOS + pain group provide valuable direction for future research and clinical care. I believe physicians should incorporate pain score assessments into their clinical practice to improve patient's quality of life and raise awareness about pain management. If future research focuses on the mechanisms of pain, it would provide a better understanding of pain and allow for a focus on the underlying causes rather than just symptomatic management. The study also highlights the association between PCOS+pain and various comorbidities, such as obesity, hypertension, and type 2 diabetes, as well as conditions like infertility and ovarian cysts, offering a holistic view of the burden of PCOS.

Weaknesses:

Due to the nature of the retrospective study, some data may not be readily available in the system. Instead of simply categorizing participants based on whether they experience pain, it would be more useful to employ a pain scale or questionnaire to better understand the severity and type of patients' pain. This approach would allow for a more thorough analysis of pain improvement following treatment with the three widely used medications for PCOS. Additionally, it would be beneficial for the authors to specify subtypes of the disease rather than generalizing conditions, such as mentioning specific digestive system disorders or mental health disorders. The lack of detailed analysis of specific disorders limits the depth of the findings. This may cause authors to make incorrect conclusions.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This retrospective study provides new data regarding the prevalence of pain in women with PCOS and its relationship with health outcomes. Using data from electronic health records (EHR), the authors found a significantly higher prevalence of pain among women with PCOS compared to those without the condition: 19.21% of women with PCOS versus 15.8% in non-PCOS women. The highest prevalence of pain was conducted among Black or African American (32.11%) and White (30.75%) populations. Besides, women with PCOS and pain have at least a 2-fold increased prevalence of obesity (34.68%) at baseline compared to women with PCOS in general (16.11%). Also, women with PCOS had the highest risk for infertility and T2D, but women with PCOS and pain had higher risks for ovarian cysts and liver disease. Regarding these results, the authors suggested the critical need to address pain in the diagnosis and management of PCOS due to its significant impact on patient health outcomes.

Strengths:

(1) The problem of pain assessment in PCOS patients is well described and the authors provided a clear rationale selection of the retrospective design to investigate this problem.(2) A large number of analyzed patient records (76,859,666 women) and their uniformity increases the power of the study. Using the Propensity Score Matching makes it possible to reduce the heterogeneity of the compared cohorts and the influence of comorbid conditions.(3) Analysis in different ethnic cohorts provides actual and necessary data regarding the prevalence of pain and its relationship with different health conditions that will be helpful for clinicians to make a diagnosis and manage PCOS in women of different ethnicities. (4) Assessment of the risk of different health conditions including PCOS-associated pathology as other common groups of diseases in PCOS women with or without pain allows to differentiate the risk of comorbid conditions depending on the presence of one symptom (pelvic or abdominal pain, dysmenorrhea).

We appreciate the positive feedback on this manuscript. Pain assessment in women with PCOS is of paramount interest and because of a gap in this research area, we are trying to address it.

Weaknesses:

(1) Although the paper has strengths in methodology and data analysis, it also has some weaknesses.

The lack of a hypothesis doesn't allow us to evaluate the aim and significance of this study.

We would like to thank the Reviewer for their valuable feedback regarding the hypothesis of this study. We understand that the hypothesis may not have been written clearly under the objectives and we will correct this in the formal revision.

The primary hypothesis of this study is that women with PCOS experience a higher prevalence to pain (including dysmenorrhea, abdominal pain and pelvic pain) compared to women without PCOS, and this prevalence varies by racial groups. Our hypothesis aims to explore the relationship between PCOS and pain, the associated health risks, and the potential racial disparities in pain prevalence and long-term health outcomes. Additionally, we seek to assess the effect of treatment on reducing pain symptoms in women with PCOS. This study not only examines the immediate burden of pain but also investigates its long-term consequences, including risks of infertility, obesity, and type 2 diabetes.

To enhance clarity for readers, we will explicitly state this hypothesis in the revised manuscript and ensure that its connection to the study’s objectives is clearly articulated. We appreciate the Reviewer’s insights and will incorporate these refinements to strengthen the manuscript.

(2) The exclusion criteria don't include conditions, that can lead to symptoms similar to PCOS: thyroid diseases, hyperprolactinemia, and congenital adrenal hyperplasia. Thyroid status is not being taken into account in the criteria for matching. All these conditions could occur as on prevalence results as on risk assessment.

We would like to thank the Reviewer for highlighting the need to include these additional conditions that mimic PCOS. After excluding hypothyroidism, hyperprolactinemia, and adrenal hyperplasia from the PCOS and PCOS and pain cohorts, we observed that 7,690 patients (1.65%) with PCOS and 1,854 patients (1.36%) with PCOS were removed. Based on this observation, we plan to add these three conditions to our exclusion criteria and rerun our analysis for disease prevalence and relative risk for our resubmission.

We will update the manuscript accordingly to reflect these exclusions and ensure clarity in our methodology. Additionally, we will discuss the rationale for excluding these conditions to improve transparency and provide a more precise interpretation of our findings.

(3) The significant weakness of the study is the absence of a Latin American cohort. Probably the White cohort includes Latin Americans or others, but the results of the study cannot be extrapolated to particular White ethnicities.

We appreciate the Reviewer’s suggestion to include Latin American cohorts in studies. In this paper we only used race as a variable and did not incorporate ethnicity. However, for our resubmission we plan to include self-reported ethnicity in our analysis which will capture the Latin American cohort stratified by self-reported race groups. This addition will provide a more comprehensive understanding of racial and ethnic differences in our study population, and we will update the manuscript accordingly to reflect this expansion.

(4) The authors didn't provide sufficient rationale for future health outcomes and this list didn't include diseases of the digestive system or disorders of thyroid glands, which can also cause abdominal pain.

We appreciate the Reviewer comment and understand their concern. Our current results highlight the prevalence of disorders of the digestive system in Figure 2 and in the results section. To further strengthen our analysis, we plan to include disorders of the digestive system in our relative risk (RR) assessment. However, we will not be able to include the same analysis for thyroid dysfunctions as they will be considered as an exclusion criterion. These updates will be incorporated into the revised manuscript to ensure clarity and completeness.

Reviewer #2 (Public review):

Summary:

The study offers a thorough analysis of the prevalence of pain in women with polycystic ovary syndrome (PCOS) and its associations with health outcomes across various racial groups. Furthermore, the research investigates the prevalence of PCOS and pain among different racial demographics, as well as the increased risk of developing various conditions in comparison to individuals who have PCOS alone.

Strengths:

The study emphasizes pain as a significant comorbidity of PCOS, an area that is critically underexplored in existing literature. The findings regarding the increased prevalence of some of the diseases in the PCOS + pain group provide valuable direction for future research and clinical care. I believe physicians should incorporate pain score assessments into their clinical practice to improve patient's quality of life and raise awareness about pain management. If future research focuses on the mechanisms of pain, it would provide a better understanding of pain and allow for a focus on the underlying causes rather than just symptomatic management. The study also highlights the association between PCOS+pain and various comorbidities, such as obesity, hypertension, and type 2 diabetes, as well as conditions like infertility and ovarian cysts, offering a holistic view of the burden of PCOS.

We sincerely appreciate the Reviewer’s insightful comments. We hope that our findings will encourage further research on the occurrence of pain in women with PCOS and that others will replicate our results to strengthen the evidence in this area. As noted in our introduction, there are currently no standardized abdominal pain score assessments specifically for women with PCOS. We hope that the findings from this study will contribute to efforts toward developing a standardized pain assessment for the PCOS community. In the meantime, further research across more diverse populations will be essential to build a more comprehensive understanding of this issue.

Weaknesses:

Due to the nature of the retrospective study, some data may not be readily available in the system. Instead of simply categorizing participants based on whether they experience pain, it would be more useful to employ a pain scale or questionnaire to better understand the severity and type of patients' pain. This approach would allow for a more thorough analysis of pain improvement following treatment with the three widely used medications for PCOS. Additionally, it would be beneficial for the authors to specify subtypes of the disease rather than generalizing conditions, such as mentioning specific digestive system disorders or mental health disorders. The lack of detailed analysis of specific disorders limits the depth of the findings. This may cause authors to make incorrect conclusions.

We appreciate the Reviewer for highlighting the importance of categorizing pain levels experienced by women with PCOS. However, there is currently no standardized pain assessment for abdominal pain, and therefore more research is required before such a classification can be made. Additionally, the electronic health record data we leveraged via the TriNextX platform does not include any pain scale data from unstructured notes. Despite these limitations, this study is an important step toward recognizing abdominal and pelvic pain in women with PCOS. Our findings indicate that women with PCOS report abdominal pain independent of digestive conditions such as irritable bowel syndrome— a condition often associated with pain in this population.

We would like to thank the Reviewer for their thoughtful comment with respect to subtyping the future health outcomes. To address this, we plan to include the most common diseases associated with PCOS for each general disease group as a supplemental figure in the revised manuscript.

eLife Assessment

This valuable study characterises the activity of motor units from two of the three anatomical subdivisions ("heads") of the triceps muscle while mice walked on a treadmill at various speeds. Although this is the most thorough characterisation of motor unit activity in walking mice to date, the evidence supporting some of the claims, especially pertaining to probabilistic recruitment of motor units, is incomplete. Further investigating whether the differences in motor unit recruitment across muscle heads go beyond their different mechanical functions would also strengthen the paper.

Reviewer #1 (Public review):

Summary:

Here, the authors have addressed the recruitment and firing patterns of motor units (MUs) from the long and lateral heads of the triceps in the mouse. They used their newly developed Myomatrix arrays to record from these muscles during treadmill locomotion at different speeds, and they used template-based spike sorting (Kilosort) to extract units. Between MUs from the two heads, the authors observed differences in their firing rates, recruitment probability, phase of activation within the locomotor cycle, and interspike interval patterning. Examining different walking speeds, the authors find increases in both recruitment probability and firing rates as speed increases. The authors also observed differences in the relation between recruitment and the angle of elbow extension between motor units from each head. These differences indicate meaningful variation between motor units within and across motor pools and may reflect the somewhat distinct joint actions of the two heads of triceps.

Strengths:

The extraction of MU spike timing for many individual units is an exciting new method that has great promise for exposing the fine detail in muscle activation and its control by the motor system. In particular, the methods developed by the authors for this purpose seem to be the only way to reliably resolve single MUs in the mouse, as the methods used previously in humans and in monkeys (e.g. Marshall et al. Nature Neuroscience, 2022) do not seem readily adaptable for use in rodents.

The paper provides a number of interesting observations. There are signs of interesting differences in MU activation profiles for individual muscles here, consistent with those shown by Marshall et al. It is also nice to see fine-scale differences in the activation of different muscle heads, which could relate to their partially distinct functions. The mouse offers greater opportunities for understanding the control of these distinct functions, compared to the other organisms in which functional differences between heads have previously been described.

The Discussion is very thorough, providing a very nice recounting of a great deal of relevant previous results.

Weaknesses:

The findings are limited to one pair of muscle heads. While an important initial finding, the lack of confirmation from analysis of other muscles acting at other joints leaves the general relevance of these findings unclear.

While differences between muscle heads with somewhat distinct functions are interesting and relevant to joint control, differences between MUs for individual muscles, like those in Marshall et al., are more striking because they cannot be attributed potentially to differences in each head's function. The present manuscript does show some signs of differences for MUs within individual heads: in Figure 2C, we see what looks like two clusters of motor units within the long head in terms of their recruitment probability. However, a statistical basis for the existence of two distinct subpopulations is not provided, and no subsequent analysis is done to explore the potential for differences among MUs for individual heads.

The statistical foundation for some claims is lacking. In addition, the description of key statistical analysis in the Methods is too brief and very hard to understand. This leaves several claims hard to validate.

Reviewer #2 (Public review):

The present study, led by Thomas and collaborators, aims to describe the firing activity of individual motor units in mice during locomotion. To achieve this, they implanted small arrays of eight electrodes in two heads of the triceps and performed spike sorting using a custom implementation of Kilosort. Simultaneously, they tracked the positions of the shoulder, elbow, and wrist using a single camera and a markerless motion capture algorithm (DeepLabCut). Repeated one-minute recordings were conducted in six mice at five different speeds, ranging from 10 to 27.5 cm·s⁻¹.

From these data, the authors reported that:

(1) a significant portion of the identified motor units was not consistently recruited across strides,<br /> (2) motor units identified from the lateral head of the triceps tended to be recruited later than those from the long head,<br /> (3) the number of spikes per stride and peak firing rates were correlated in both muscles, and<br /> (4) the probability of motor unit recruitment and firing rates increased with walking speed.

The authors conclude that these differences can be attributed to the distinct functions of the muscles and the constraints of the task (i.e., speed).

Strengths:

The combination of novel electrode arrays to record intramuscular electromyographic signals from a larger muscle volume with an advanced spike sorting pipeline capable of identifying populations of motor units.

Weaknesses:

(1) There is a lack of information on the number of identified motor units per muscle and per animal.

(2) All identified motor units are pooled in the analyses, whereas per-animal analyses would have been valuable, as motor units within an individual likely receive common synaptic inputs. Such analyses would fully leverage the potential of identifying populations of motor units.

(3) The current data do not allow for determining which motor units were sampled from each pool. It remains unclear whether the sample is biased toward high-threshold motor units or representative of the full pool.

(4) The behavioural analysis of the animals relies solely on kinematics (2D estimates of elbow angle and stride timing). Without ground reaction forces or shoulder angle data, drawing functional conclusions from the results is challenging.

Major comments:

(1) Spike sorting

The conclusions of the study rely on the accuracy and robustness of the spike sorting algorithm during a highly dynamic task. Although the pipeline was presented in a previous publication (Chung et al., 2023, eLife), a proper validation of the algorithm for identifying motor unit spikes is still lacking. This is particularly important in the present study, as the experimental conditions involve significant dynamic changes. Under such conditions, muscle geometry is altered due to variations in both fibre pennation angles and lengths.

This issue differs from electrode drift, and it is unclear whether the original implementation of Kilosort includes functions to address it. Could the authors provide more details on the various steps of their pipeline, the strategies they employed to ensure consistent tracking of motor unit action potentials despite potential changes in action potential waveforms, and the methods used for manual inspection of the spike sorting algorithm's output?

(2) Yield of the spike sorting pipeline and analyses per animal/muscle

A total of 33 motor units were identified from two heads of the triceps in six mice (17 from the long head and 16 from the lateral head). However, precise information on the yield per muscle per animal is not provided. This information is crucial to support the novelty of the study, as the authors claim in the introduction that their electrode arrays enable the identification of populations of motor units.

Beyond reporting the number of identified motor units, another way to demonstrate the effectiveness of the spike sorting algorithm would be to compare the recorded EMG signals with the residual signal obtained after subtracting the action potentials of the identified motor units, using a signal-to-residual ratio.

Furthermore, motor units identified from the same muscle and the same animal are likely not independent due to common synaptic inputs. This dependence should be accounted for in the statistical analyses when comparing changes in motor unit properties across speeds and between muscles.

(3) Representativeness of the sample of identified motor units

However, to draw such conclusions, the authors should exclusively compare motor units from the same pool and systematically track violations of the recruitment order. Alternatively, they could demonstrate that the motor units that are intermittently active across strides correspond to the smallest motor units, based on the assumption that these units should always be recruited due to their low activation thresholds.

One way to estimate the size of motor units identified within the same muscle would be to compare the amplitude of their action potentials, assuming that all motor units are relatively close to the electrodes (given the selectivity of the recordings) and that motoneurons innervating more muscle fibres generate larger motor unit action potentials.

Currently, the data seem to support the idea that motor units that are alternately recruited across strides have recruitment thresholds close to the level of activation or force produced during slow walking. The fact that recruitment probability monotonically increases with speed suggests that the force required to propel the mouse forward exceeds the recruitment threshold of these "large" motor units. This pattern would primarily reflect spatial recruitment following the size principle rather than flexible motor unit control.

(4) Analysis of recruitment and firing rates

The authors currently report active duration and peak firing rates based on spike trains convolved with a Gaussian kernel. Why not report the peak of the instantaneous firing rates estimated from the inverse of the inter-spike interval? This approach appears to be more aligned with previous studies conducted to describe motor unit behaviour during fast movements (e.g., Desmedt & Godaux, 1977, J Physiol; Van Cutsem et al., 1998, J Physiol; Del Vecchio et al., 2019, J Physiol).

(5) Additional analyses on behaviour

The authors currently analyse motor unit recruitment in relation to elbow angle. It would be valuable to include a similar analysis using the angular velocity observed during each stride, as higher velocity would place each muscle in a less favourable position on the force-velocity relationship for generating the required force. More broadly, comparing stride-by-stride changes in firing rates with changes in elbow angular velocity would further strengthen the final analyses presented in the results section.

Reviewer #3 (Public review):

Summary:

Using the approach of Myomatrix recording, the authors report that:

(1) Motor units are recruited differently in the two types of muscles.<br /> (2) Individual units are probabilistically recruited during the locomotion strides, whereas the population bulk EMG has a more reliable representation of the muscle.<br /> (3) The recruitment of units was proportional to walking speed.

Strengths:

The new technique provides a unique data set, and the data analysis is convincing and well-performed.

Weaknesses:

The implications of "probabilistical recruitment" should be explored, addressed, and analyzed further.

Comments:

One of the study's main findings (perhaps the main finding) is that the motor units are "probabilistically" recruited. The authors do not define what they mean by probabilistically recruited, nor do they present an alternative scenario to such recruitment or discuss why this would be interesting or surprising. However, on page 4, they do indicate that the recruitment of units from both muscles was only active in a subset of strides, i.e., they are not reliably active in every step.

If probabilistic means irregular spiking, this is not new. Variability in spiking has been seen numerous times, for instance in human biceps brachii motor units during isometric contractions (Pascoe, Enoka, Exp physiology 2014) and elsewhere. Perhaps the distinction the authors are seeking is between fluctuation-driven and mean-driven spiking of motor units as previously identified in spinal motor networks (see Petersen and Berg, eLife 2016, and Berg, Frontiers 2017). Here, it was shown that a prominent regime of irregular spiking is present during rhythmic motor activity, which also manifests as a positive skewness in the spike count distribution (i.e., log-normal).

eLife Assessment

This important study identifies a novel role for Hes5+ astrocytes in modulating the activity of descending pain-inhibitory noradrenergic neurons from the locus coeruleus during stress-induced pain facilitation. The role of glia in modulating neurological circuits including pain is poorly understood, and in that light, the role of Hes5+ astrocytes in this circuit is a key finding with broader potential impacts. However, the impact of this work is limited by incomplete evidence, notably the fact that acute restraint stress is generally anti-nociceptive rather than pro-nociceptive, and a lack of specificity in defining this novel circuit.

Reviewer #1 (Public review):

Summary

In this article, Kawanabe-Kobayashi et al., aim to examine the mechanisms by which stress can modulate pain in mice. They focus on the contribution of noradrenergic neurons (NA) of the locus coeruleus (LC). The authors use acute restraint stress as a stress paradigm and found that following one hour of restraint stress mice display mechanical hypersensitivity. They show that restraint stress causes the activation of LC NA neurons and the release of NA in the spinal cord dorsal horn (SDH). They then examine the spinal mechanisms by which LC→SDH NA produces mechanical hypersensitivity. The authors provide evidence that NA can act on alphaA1Rs expressed by a class of astrocytes defined by the expression of Hes (Hes+). Furthermore, they found that NA, presumably through astrocytic release of ATP following NA action on alphaA1Rs Hes+ astrocytes, can cause an adenosine-mediated inhibition of SDH inhibitory interneurons. They propose that this disinhibition mechanism could explain how restraint stress can cause the mechanical hypersensitivity they measured in their behavioral experiments.

Strengths:

(1) Significance. Stress profoundly influences pain perception; resolving the mechanisms by which stress alters nociception in rodents may explain the well-known phenomenon of stress-induced analgesia and/or facilitate the development of therapies to mitigate the negative consequences of chronic stress on chronic pain.

(2) Novelty. The authors' findings reveal a crucial contribution of Hes+ spinal astrocytes in the modulation of pain thresholds during stress.

(3) Techniques. This study combines multiple approaches to dissect circuit, cellular, and molecular mechanisms including optical recordings of neural and astrocytic Ca2+ activity in behaving mice, intersectional genetic strategies, cell ablation, optogenetics, chemogenetics, CRISPR-based gene knockdown, slice electrophysiology, and behavior.

Weaknesses:

(1) Mouse model of stress. Although chronic stress can increase sensitivity to somatosensory stimuli and contribute to hyperalgesia and anhedonia, particularly in the context of chronic pain states, acute stress is well known to produce analgesia in humans and rodents. The experimental design used by the authors consists of a single one-hour session of restraint stress followed by 30 min to one hour of habituation and measurement of cutaneous mechanical sensitivity with von Frey filaments. This acute stress behavioral paradigm corresponds to the conditions in which the clinical phenomenon of stress-induced analgesia is observed in humans, as well as in animal models. Surprisingly, however, the authors measured that this acute stressor produced hypersensitivity rather than antinociception. This discrepancy is significant and requires further investigation.

(2) Specifically, is the hypersensitivity to mechanical stimulation also observed in response to heat or cold on a hotplate or coldplate?

(3) Using other stress models, such as a forced swim, do the authors also observe acute stress-induced hypersensitivity instead of stress-induced antinociception?

(4) Measurement of stress hormones in blood would provide an objective measure of the stress of the animals.

(5) Results:

a) Optical recordings of Ca2+ activity in behaving rodents are particularly useful to investigate the relationship between Ca2+ dynamics and the behaviors displayed by rodents.

b) The authors report an increase in Ca2+ events in LC NA neurons during restraint stress: Did mice display specific behaviors at the time these Ca2+ events were observed such as movements to escape or orofacial behaviors including head movements or whisking?

c) Additionally, are similar increases in Ca2+ events in LC NA neurons observed during other stressful behavioral paradigms versus non-stressful paradigms?

d) Neuronal ablation to reveal the function of a cell population.

e) The proportion of LC NA neurons and LC→SDH NA neurons expressing DTR-GFP and ablated should be quantified (Figures 1G and J) to validate the methods and permit interpretation of the behavioral data (Figures 1H and K). Importantly, the nocifensive responses and behavior of these mice in other pain assays in the absence of stress (e.g., hotplate) and a few standard assays (open field, rotarod, elevated plus maze) would help determine the consequences of cell ablation on processing of nociceptive information and general behavior.

f) Confirmation of LC NA neuron function with other methods that alter neuronal excitability or neurotransmission instead of destroying the circuit investigated, such as chemogenetics or chemogenetics, would greatly strengthen the findings. Optogenetics is used in Figure 1M, N but excitation of LC→SDH NA neuron terminals is tested instead of inhibition (to mimic ablation), and in naïve mice instead of stressed mice.

g) Alpha1Ars. The authors noted that "Adra1a mRNA is also expressed in INs in the SDH".

h) The authors should comprehensively indicate what other cell types present in the spinal cord and neurons projecting to the spinal cord express alpha1Ars and what is the relative expression level of alpha1Ars in these different cell types.

i) The conditional KO of alpha1Ars specifically in Hes5+ astrocytes and not in other cell types expressing alpha1Ars should be quantified and validated (Figure 2H).

j) Depolarization of SDH inhibitory interneurons by NA (Figure 3). The authors' bath applied NA, which presumably activates all NA receptors present in the preparation.

k) The authors' model (Figure 4H) implies that NA released by LC→SDH NA neurons leads to the inhibition of SDH inhibitory interneurons by NA. In other experiments (Figure 1L, Figure 2A), the authors used optogenetics to promote the release of endogenous NA in SDH by LC→SDH NA neurons. This approach would investigate the function of NA endogenously released by LC NA neurons at presynaptic terminals in the SDH and at physiological concentrations and would test the model more convincingly compared to the bath application of NA.

l) As for other experiments, the proportion of Hes+ astrocytes that express hM3Dq, and the absence of expression in other cells, should be quantified and validated to interpret behavioral data.

m) Showing that the effect of CNO is dose-dependent would strengthen the authors' findings.

n) The proportion of SG neurons for which CNO bath application resulted in a reduction in recorded sIPSCs is not clear.

o) A1Rs. The specific expression of Cas9 and guide RNAs, and the specific KD of A1Rs, in inhibitory interneurons but not in other cell types expressing A1Rs should be quantified and validated.

(6) Methods:

It is unclear how fiber photometry is performed using "optic cannula" during restraint stress while mice are in a 50ml falcon tube (as shown in Figure 1A).

Reviewer #2 (Public review):

Summary:

This study investigates the role of spinal astrocytes in mediating stress-induced pain hypersensitivity, focusing on the LC (locus coeruleus)-to-SDH (spinal dorsal horn) circuit and its mechanisms. The authors aimed to delineate how LC activity contributes to spinal astrocytic activation under stress conditions, explore the role of noradrenaline (NA) signaling in this process, and identify the downstream astrocytic mechanisms that influence pain hypersensitivity.

The authors provide strong evidence that 1-hour restraint stress-induced pain hypersensitivity involves the LC-to-SDH circuit, where NA triggers astrocytic calcium activity via alpha1a adrenoceptors (alpha1aRs). Blockade of alpha1aRs on astrocytes - but not on Vgat-positive SDH neurons - reduced stress-induced pain hypersensitivity. These findings are rigorously supported by well-established behavioral models and advanced genetic techniques, uncovering the critical role of spinal astrocytes in modulating stress-induced pain.

However, the study's third aim - to establish a pathway from astrocyte alpha1aRs to adenosine-mediated inhibition of SDH-Vgat neurons - is less compelling. While pharmacological and behavioral evidence is intriguing, the ex vivo findings are indirect and lack a clear connection to the stress-induced pain model. Despite these limitations, the study advances our understanding of astrocyte-neuron interactions in stress-pain contexts and provides a strong foundation for future research into glial mechanisms in pain hypersensitivity.

Strengths:

The study is built on a robust experimental design using a validated 1-hour restraint stress model, providing a reliable framework to investigate stress-induced pain hypersensitivity. The authors utilized advanced genetic tools, including retrograde AAVs, optogenetics, chemogenetics, and subpopulation-specific knockouts, allowing precise manipulation and interrogation of the LC-SDH circuit and astrocytic roles in pain modulation. Clear evidence demonstrates that NA triggers astrocytic calcium activity via alpha1aRs, and blocking these receptors effectively reduces stress-induced pain hypersensitivity.

Weaknesses:

Despite its strengths, the study presents indirect evidence for the proposed NA-to-astrocyte(alpha1aRs)-to-adenosine-to-SDH-Vgat neurons pathway, as the link between astrocytic adenosine release and stress-induced pain remains unclear. The ex vivo experiments, including NA-induced depolarization of Vgat neurons and chemogenetic stimulation of astrocytes, are challenging to interpret in the stress context, with the high CNO concentration raising concerns about specificity. Additionally, the role of astrocyte-derived D-serine is tangential and lacks clarity regarding its effects on SDH Vgat neurons. The astrocyte calcium signal "dip" after LC optostimulation-induced elevation are presented without any interpretation.

Reviewer #3 (Public review):

Summary

This is an exciting and timely study addressing the role of descending noradrenergic systems in nocifensive responses. While it is well-established that spinally released noradrenaline (aka norepinephrine) generally acts as an inhibitory factor in spinal sensory processing, this system is highly complex. Descending projections from the A6 (locus coeruleus, LC) and the A5 regions typically modulate spinal sensory processing and reduce pain behaviours, but certain subpopulations of LC neurons have been shown to mediate pronociceptive effects, such as those projecting to the prefrontal cortex (Hirshberg et al., PMID: 29027903).

The study proposes that descending cerulean noradrenergic neurons potentiate touch sensation via alpha-1 adrenoceptors on Hes5+ spinal astrocytes, contributing to mechanical hyperalgesia. This finding is consistent with prior work from the same group (dd et al., PMID:). However, caution is needed when generalising about LC projections, as the locus coeruleus is functionally diverse, with differences in targets, neurotransmitter co-release, and behavioural effects. Specifying the subpopulations of LC neurons involved would significantly enhance the impact and interpretability of the findings.

Strengths

The study employs state-of-the-art molecular, genetic, and neurophysiological methods, including precise CRISPR and optogenetic targeting, to investigate the role of Hes5+ astrocytes. This approach is elegant and highlights the often-overlooked contribution of astrocytes in spinal sensory gating. The data convincingly support the role of Hes5+ astrocytes as regulators of touch sensation, coordinated by brain-derived noradrenaline in the spinal dorsal horn, opening new avenues for research into pain and touch modulation.

Furthermore, the data support a model in which superficial dorsal horn (SDH) Hes5+ astrocytes act as non-neuronal gating cells for brain-derived noradrenergic (NA) signalling through their interaction with substantia gelatinosa inhibitory interneurons. Locally released adenosine from NA-stimulated Hes5+ astrocytes, following acute restraint stress, may suppress the function of SDH-Vgat+ inhibitory interneurons, resulting in mechanical pain hypersensitivity. However, the spatially restricted neuron-astrocyte communication underlying this mechanism requires further investigation in future studies.

Weaknesses

(1) Specificity of the LC Pathway targeting

The main concern lies with how definitively the LC pathway was targeted. Were other descending noradrenergic nuclei, such as A5 or A7, also labelled in the experiments? The authors must convincingly demonstrate that the observed effects are mediated exclusively by LC noradrenergic terminals to substantiate their claims (i.e. "we identified a circuit, the descending LC→SDH-NA neurons").

a) For instance, the direct vector injection into the LC likely results in unspecific effects due to the extreme heterogeneity of this nucleus and retrograde labelling of the A5 and A7 nuclei from the LC (i.e., Li et al., PMID: 26903420).

b) It is difficult to believe that the intersectional approach described in the study successfully targeted LC→SDH-NA neurons using AAVrg vectors. Previous studies (e.g., PMID: 34344259 or PMID: 36625030) demonstrated that similar strategies were ineffective for spinal-LC projections. The authors should provide detailed quantification of the efficiency of retrograde labelling and specificity of transgene expression in LC neurons projecting to the SDH.

c) Furthermore, it is striking that the authors observed a comparably strong phenotypical change in Figure 1K despite fewer neurons being labelled, compared to Figure 1H and 1N with substantially more neurons being targeted. Interestingly, the effect in Figure 1K appears more pronounced but shorter-lasting than in the comparable experiment shown in Figure 1H. This discrepancy requires further explanation.

d) A valuable addition would be staining for noradrenergic terminals in the spinal cord for the intersectional approach (Figure 1J), as done in Figures 1F/G. LC projections terminate preferentially in the SDH, whereas A5 projections terminate in the deep dorsal horn (DDH). Staining could clarify whether circuits beyond the LC are being ablated.

e) Furthermore, different LC neurons often mediate opposite physiological outcomes depending on their projection targets-for example, dorsal LC neurons projecting to the prefrontal cortex PFCx are pronociceptive, while ventral LC neurons projecting to the SC are antinociceptive (PMIDs: 29027903, 34344259, 36625030). Given this functional diversity, direct injection into the LC is likely to result in nonspecific effects.

Conclusion on Specificity: The authors are strongly encouraged to address these limitations directly, as they significantly affect the validity of the conclusions regarding the LC pathway. Providing more robust evidence, acknowledging experimental limitations, and incorporating complementary analyses would greatly strengthen the manuscript.

(2) Discrepancies in Data

a) Figures 1B and 1E: The behavioural effect of stress on PWT (Figure 1E) persists for 120 minutes, whereas Ca²⁺ imaging changes (Figure 1B) are only observed in the first 20 minutes, with signal attenuation starting at 30 minutes. This discrepancy requires clarification, as it impacts the proposed mechanism.

b) Figure 4E: The effect is barely visible, and the tissue resembles "Swiss cheese," suggesting poor staining quality. This is insufficient for such an important conclusion. Improved staining and/or complementary staining (e.g., cFOS) are needed. Additionally, no clear difference is observed between Stress+Ab stim. and Stress+Ab stim.+CPT, raising doubts about the robustness of the data.

c) Discrepancy with Existing Evidence: The claim regarding the pronociceptive effect of LC→SDH-NAergic signalling on mechanical hypersensitivity contrasts with findings by Kucharczyk et al. (PMID: 35245374), who reported no facilitation of spinal convergent (wide-dynamic range) neuron responses to tactile mechanical stimuli, but potent inhibition to noxious mechanical von Frey stimulation. This discrepancy suggests alternative mechanisms may be at play and raises the question of why noxious stimuli were not tested.

(3) Sole reliance on Von Frey testing

The exclusive use of von Frey as a behavioural readout for mechanical sensitisation is a significant limitation. This assay is highly variable, and without additional supporting measures, the conclusions lack robustness. Incorporating other behavioural measures, such as the adhesive tape removal test to evaluate tactile discomfort, the needle floor walk corridor to assess sensitivity to uneven or noxious surfaces, or the kinetic weight-bearing test to measure changes in limb loading during movement, could provide complementary insights. Physiological tests, such as the Randall-Selitto test for noxious pressure thresholds or CatWalk gait analysis to evaluate changes in weight distribution and gait dynamics, would further strengthen the findings and allow for a more comprehensive assessment of mechanical sensitisation.

Overall Conclusion

This study addresses an important and complex topic with innovative methods and compelling data. However, the conclusions rely on several assumptions that require more robust evidence. Specificity of the LC pathway, experimental discrepancies, and methodological limitations (e.g., sole reliance on von Frey) must be addressed to substantiate the claims. With these issues resolved, this work could significantly advance our understanding of astrocytic and noradrenergic contributions to pain modulation.

eLife Assessment

This is a useful follow-up on previous work on the same LGI1-ADAM22 complex using cross-linking to stabilize a trimeric state that the authors had previously observed by SEC-MALS and small-angle X-ray scattering (the previous crystal structure was determined in a dimeric form). A strength of this solid work is that oligomeric states do not affect the critical interaction between LGI1 and ADAM23, so the previous conclusions are still valid. A weakness is that the physiological relevance of the trimeric assembly is unclear.

Reviewer #1 (Public review):

The structure of a heterohexameric 3:3 LGI1-ADAM22 complex is resolved by Yamaguchi et al. It reveals the intermolecular LGI1 interactions and their role in bringing three ADAM22 molecules together. This may be relevant for the clustering of axonal Kv1 channels and control over their density. While it is currently not clear if the heterohexameric 3:3 LGI1-ADAM22 complex has a physiological role, the detailed structural information, presented here, allows us to pinpoint mutations or other strategies to probe the relevance of the 3:3 complex in future work.

The experimental work is done to a high standard, and I have no comments on that part. I do have several recommendations that I hope will be considered.

(1) A previously determined 2:2 heterodimeric complex of LGI1-ADAM22 was suggested to play a role in trans interactions. Could the authors discuss if the heterohexameric 3:3 LGI1-ADAM22 is more likely to represent a cis complex or a trans complex, or if both are possible?

(2) It is not entirely clear to me if the LGI1-ADAM22 complex is also crosslinked in the HS-AFM experiments. Could this be more clearly indicated? In addition, if this is the case, could an explanation be given about how the complex can still dissociate?

(3) The LGI1 and ADAM22 are of similar size. To me, this complicates the interpretation of dissociation of the complex in the HS-AFM data. How is the overinterpretation of this data prevented? In other words, what confidence do the authors have in the dissociation steps in the HS-AFM data?

(4) What is the "LGI1 collapse" mentioned in Figure 4c?

(5) Am I correct that the structure indicates that the trimerization is entirely organized by LGI1? This would suggest LGI1 trimerizes on its own. Can this be discussed? Has this been observed?

(6) C3 symmetry was not applied in the cryo-EM reconstruction of the heterohexameric 3:3 LGI1-ADAM22 complex. How much is the complex deviating from C3 symmetry? What interactions stabilize the specific trimeric conformation reconstructed here, compared to other trimeric conformations?

Reviewer #2 (Public review):

Summary:

The study by Yamaguchi et al. provides compelling evidence for the formation of a 3:3 complex between the ectodomain of ADAM22 and LGI1, as demonstrated using single-particle cryo-EM and HS-AFM. This represents the first instance in which the 3:3 complex has been resolved sufficiently to enable molecular modeling, allowing the authors to identify key interfaces mediating ADAM22-LGI1 interactions. HS-AFM revealed weak interactions within the 3:3 complexes, suggesting the dynamic nature of ADAM22-LGI1 interactions, which may play a role in modulating synaptic activity.

Strength:

A strength of this study lies in the novel identification of the 3:3 complexes, captured at an unprecedented level of resolution and validated by HS-AFM. This discovery, together with the authors' previous findings demonstrating a 2:2 stoichiometry, gives rise to an intriguing hypothesis regarding the dynamic nature of the ADAM22-LGI1 complex in regulating both cis- and trans-synaptic interactions.

Weakness:

The functional significance of these two complexes in the context of synapse remains speculative. Additionally, the structural presentations in Figures 1-3 (especially Figures 2-3) lack the clarity needed for general readers to fully understand the authors' key points. Enhancing the quality of these visual representations would greatly improve accessibility and comprehension.

eLife Assessment

This paper presents the important finding that BNIP3/NIX, a mitophagy receptor, and its binding to ATG18 are required for mitophagy during muscle cell reorganization in Drosophila. Although the involvement of the BNIP3-ATG18/WIPI axis in mitophagy induction has been reported in mammalian cell culture systems, this study provides the first compelling evidence for this pathway in vivo in animals. The physiological significance of this BNIP3-dependent mitophagy will require further investigation.

Reviewer #1 (Public review):

Summary:

During early Drosophila pupal development, a subset of larval abdominal muscles (DIOMs) is remodelled using an autophagy-dependent mechanism.

To better understand this not very well studied process, the authors have generated a transcriptomics time course using dissected abdominal muscles of various stages from wild-type and autophagy-deficient mutants. The authors have further identified a function for BNIP3 in muscle mitophagy using this system.

Strengths:

(1) The paper does provide a detailed mRNA time course resource for DIOM remodelling.

(2) The paper does find an interesting BNIP3 loss of function phenotype, a block of mitophagy during muscle remodelling, and hence identifies a specific linker between mitochondria and the core autophagy machinery. This adds to the mechanism of how mitochondria are degraded.

(3) Sophisticated fly genetics demonstrates that the larval muscle mitochondria are, to a large extent, degraded by autophagy during DIOM remodelling.

Weaknesses:

(1) Mitophagy during DIOM remodelling is not novel (earlier papers from Fujita et al.).

(2) The transcriptomics time course data are not well connected to the autophagy part. Both could be separated into 2 independent manuscripts.

(3) The muscle phenotypes need better quantifications, both for the EM and light microscopy data in various figures.

(4)The transcriptomics data are hard to browse in the provided PDF format.

Reviewer #2 (Public review):

Summary:

Autophagy (macroautophagy) is known to be essential for muscle function in flies and mammals. To date, many mitophagy (selective mitochondrial autophagy) receptors have been identified in mammals and other species. While the loss of mitophagy receptors has been shown to impair mitochondrial degradation (e.g., OPTN and NDP52 in Parkin-mediated mitophagy and NIX and BNIP3 in hypoxia-induced mitophagy) at the level of cultured cells, it remains unclear, especially under physiological conditions in vivo. In this study, the authors revealed that one of the receptors BNIP3 plays a critical role in mitochondrial degradation during muscle remodeling in vivo.

Overall, the manuscript provides solid evidence that BNIP3 is involved in mitophagy during muscle remodeling with in vivo analyses performed. In particular, all experiments in this study are well-designed. The text is well written and the figures are very clear.

Strengths:

(1) In each experiment, appropriate positive and negative controls are used to indicate what is responsible for the phenomenon observed by the authors: e.g. FIP200, Atg18, Stx17 siRNAs during DIOM remodeling in Figure 2 and Full, del-LIR, del-MER in Figure 5.

(2) Although the transcriptional dynamics of DIOM remodeling during metamorphosis is autophagy-independent, the transcriptome data obtained by the authors would be valuable for future studies.

(3) In addition to the simple observation that loss of BNIP3 causes mitochondrial accumulation, the authors further observed that, by combining siRNA against STX17, which is required for fusion of autophagosomes with lysosomes, BNIP3 KO abolishes mitophagosome formation, which will provide solid evidence for BNIP3-mediated mitophagy. Furthermore, using a Gal80 temperature-sensitive approach, the authors showed that mitochondria derived from larval muscle, but not those synthesized during hypertrophy, remain in BNIP3 KO fly muscles.

Weaknesses:

(1) Because BNIP3 KO causes mitochondrial accumulation, it is expected that adult flies will have some physiological defects, but this has not been fully analyzed or sufficiently mentioned in the manuscript.

(2) In Figure 5, the authors showed that BNIP3 binds to Atg18a by co-IP, but no data are provided on whether MER-mut or del-MER attenuates the affinity for Atg18a.

Reviewer #3 (Public review):

Summary:

Fujita et al build on their earlier, 2017 eLife paper that showed the role of autophagy in the developmental remodeling of a group of muscles (DIOM) in the abdomen of Drosophila. Most larval muscles undergo histolysis during metamorphosis, while DIOMs are programmed to regrow after initial atrophy to give rise to temporary adult muscles, which survive for only 1 day after eclosion of the adult flies (J Neurosci. 1990;10:403-1. and BMC Dev Biol 16, 12, 2016). The authors carry out transcriptomics profiling of these muscles during metamorphosis, which is in agreement with the atrophy and regrowth phases of these muscles. Expression of the known mitophagy receptor BNIP3/NIX is high during atrophy, so the authors have started to delve more into the role of this protein/mitophagy in their model. BNIP3 KO indeed impairs mitophagy and muscle atrophy, which they convincingly demonstrate via nice microscopy images. They also show that the already known Atg8a-binding LIR and Atg18a-binding MER motifs of human NIX are conserved in the Drosophila protein, although the LIR turned out to be less critical for in vivo protein function than the MER motif.

Strengths:

Established methodology, convincing data, in vivo model.

Weaknesses:

The significance for Drosophila physiology and for human muscles remains to be established.

eLife Assessment

This paper provides a compelling and rigorous quantitative analysis of the turnover and maintenance of CD4+ tissue-resident memory T cell clones, in the skin and the lamina propria. It provides a fundamental advance in our understanding of CD4 T cell regulation. Interestingly, in both tissues, maintenance involves an influx from progenitors on the time scale of months. The evidence that is based on fate mapping and mathematical inference is strong, although open questions on the interpretation of the Ki67-based fate mapping remain.

Reviewer #1 (Public review):

Summary:

Compelling and clearly described work that combines two elegant cell fate reporter strains with mathematical modelling to describe the kinetics of CD4+ TRM in mice. The aim is to investigate the cell dynamics underlying the maintenance of CD4+TRM.

The main conclusions are that:<br /> (1) CD4+ TRM are not intrinsically long-lived.<br /> (2) Even clonal half-lives are short: 1 month for TRM in skin, and even shorter (12 days) for TRM in lamina propria.<br /> (3) TRM are maintained by self-renewal and circulating precursors.

Strengths:

(1) Very clearly and succinctly written. Though in some places too succinctly! See suggestions below for areas I think could benefit from more detail.

(2) Powerful combination of mouse strains and modelling to address questions that are hard to answer with other approaches.

(3) The modelling of different modes of recruitment (quiescent, neutral, division linked) is extremely interesting and often neglected (for simpler neutral recruitment).

Weaknesses/scope for improvement:

(1) The authors use the same data set that they later fit for generating their priors. This double use of the same dataset always makes me a bit squeamish as I worry it could lead to an underestimate of errors on the parameters. Could the authors show plots of their priors and posteriors to check that the priors are not overly-influential? Also, how do differences in priors ultimately influence the degree of support a model gets (if at all)? Could differences in priors lead to one model gaining more support than another?

(2) The authors state (line 81) that cells were "identified as tissue-localised by virtue of their protection from short-term in vivo labelling (Methods; Fig. S1B)". I would like to see more information on this. How short is short term? How long after labelling do cells need to remain unlabelled in order to be designated tissue-localised (presumably label will get to tissue pretty quickly -within hours?). Can the authors provide citations to defend the assumption that all label-negative cells are tissue-localised (no false negatives)? And conversely that no label-positive cells can be found in the tissue (no false positives)? I couldn't actually find the relevant section in the methods and Figure S1B didn't contain this information.

(3) Are the target and precursor populations from the same mice? If so is there any way to reflect the between-individual variation in the precursor population (not captured by the simple empirical fit)? I am thinking particularly of the skin and LP CD4+CD69- populations where the fraction of cells that are mTOM+ (and to a lesser extent YFP+) spans virtually the whole range. Would it be nice to capture this information in downstream predictions if possible?

(4) In Figure 3, estimates of kinetics for cells in LP appear to be more dependent on the input model (quiescent/neutral/division-linked) than the same parameters in the skin. Can the authors explain intuitively why this is the case?

(5) Can the authors include plots of the model fits to data associated with the different strengths of support shown in Figure 4? That is, I would like to know what a difference in the strength of say 0.43 compared with 0.3 looks like in "real terms". I feel strongly that this is important. Are all the fits fantastic, and some marginally better than others? Are they all dreadful and some are just less dreadful? Or are there meaningful differences?

(6) Figure 4 left me unclear about exactly which combinations of precursors and targets were considered. Figure 3 implies there are 5 precursors but in Figure 4A at most 4 are considered. Also, Figure 4B suggests skin CD69- were considered a target. This doesn't seem to be specified anywhere.

Reviewer #2 (Public review):

This manuscript addresses a fundamental problem of immunology - the persistence mechanisms of tissue-resident memory T cells (TRMs). It introduces a novel quantitative methodology, combining the in vivo tracing of T-cell cohorts with rigorous mathematical modeling and inference. Interestingly, the authors show that immigration plays a key role in maintaining CD4+ TRM populations in both skin and lamina propria (LP), with LP TRMs being more dependent on immigration than skin TRMs. This is an original and potentially impactful manuscript. However, several aspects were not clear and would benefit from being explained better or worked out in more detail.

(1) The key observations are as follows:

a) When heritably labeling cells due to CD4 expression, CD4+ TRM labeling frequency declines with time. This implies that CD4+ TRMs are ultimately replenished from a source not labeled, hence not expressing CD4. Most likely, this would be DN thymocytes.

b) After labeling by Ki67 expression, labeled CD4+ TRMs also decline - This is what Figure 1B suggests. Hence they would be replaced by a source that was not in the cell cycle at the time of labeling. However, is this really borne out by the experimental data (Figure 2C, middle row)? Please clarify.

(2) For potential source populations (Figure 2D): Please discuss these data critically. For example, CD4+ CD69- cells in skin and LP start with a much lower initial labeling frequency than the respective TRM populations. Could the former then be precursors of the latter? A similar question applies to LN YFP+ cells. Moreover, is the increase in YFP labeling in naïve T cells a result of their production from proliferative thymocytes? How well does the quantitative interpretation of YFP labeling kinetics in a target population work when populations upstream show opposite trends (e.g., naïve T cells increasing in YFP+ frequency but memory cells in effect decreasing, as, at the time of labeling, non-activated = non-proliferative T cells (and hence YFP-) might later become activated and contribute to memory)?

(3) Please add a measure of variation (e.g., suitable credible intervals) to the "best fits" (solid lines in Figure 2).

(4) Could the authors better explain the motivation for basing their model comparisons on the Leave-One-Out (LOO) cross-validation method? Why not use Bayesian evidence instead?

eLife Assessment

This study approaches an important topic providing insight into the neuronal circuitry that interconnects memory consolidation and sleep. The data were collected and analysed using a solid methodology, contributing new findings for neurobiologists working on how memories are stored and the roles of sleep. However, the data is incomplete to support the proposed role of the PAM-DPM circuits as the link between sleep state and long-term memory consolidation.

Reviewer #1 (Public review):

Summary:

The authors aim to use state-of-the art behaviour, imaging, and connectome techniques to identify the neural interaction between sleep and long-term memory consolidation in the PAM-DPM circuits, a well-known dopaminergic pathway within Drosophila Mushroom Body.

Strengths:

From a Drosophila sleep researcher's perspective, the investigation follows a clear and logical strategy to collect a huge dataset of sleep, appetitive memory, and live imaging. The authors clearly identified and showed that activation of a PAM subset: alpha-1 reduces sleep quality and memory consolidation in a starvation-dependent manner. The authors also convincingly demonstrated the corresponding neuronal responses of DPM neurons following PAM alpha-1 activation, and the positive role of DPM neural activity in sleep and memory consolidation. Moreover, the authors applied a new way of sleep statistics to demonstrate hour-by-hour changes between treatment and genotypes. Importantly, the authors demonstrated that memory loss derived from PAM alpha 1 activation can be partly restored by ectopic sleep enhancement via feeding THIP during the memory consolidation period after training.

Weaknesses:

Two investigatory gaps relate to the misalignment between circuital activity and behaviours, due to the nature of large circuital functional analysis like this. Firstly, the central observation of the study indicates that PAM alpha1 activation causes DPM inhibition which disrupts sleep and memory consolidation. Therefore one would expect a reduced PAMalpha1 and increased DPM activities after memory training, but the authors found that the endogenous CRTC::GFP reported neuronal activity for PAMalpha1 and DPM are both increased after memory training (Figure 9). This can be due to the difficult functional demarcation among the 14 PAMalpha1 projections. Secondly, the authors acknowledged the contradicting finding that memory defect is detected in PAMalpha1 inactivation (Figure 7C), yet suggested a tight link between sleep and memory consolidation; it is clear loss of PAM subset activity can disrupt memory consolidation without affecting sleep (cf Figure 7C and 7I).

Reviewer #2 (Public review):

Summary:

Sleep plays a critical role in memory consolidation, but the neural mechanisms underlying this relationship remain poorly understood. The authors present novel findings implicating two small neuronal groups with inhibitory connections, PAM-a1 to DPM, in sleep regulation and LTM consolidation. However, whether the PAM-a1 to DPM microcircuit promotes LTM consolidation through sleep regulation requires further investigation.

Strengths:

The authors report several novel findings. Brief activation or inhibition of PAM-a1 neurons, or brief inhibition of DPM neurons during the first few hours after training, impairs 24-hour LTM. Notably, these brief manipulations disrupt sleep for many hours afterward, particularly at night. Interestingly, disruption of PAM-a1 and DPM neurons impairs sleep and appetitive memory consolidation only under starvation conditions, and pharmacological induction of sleep during the night rescues the LTM defects. These findings suggest that PAM-a1 and DPM neurons are involved in sleep regulation and LTM consolidation under starvation. These are important findings that advance our understanding of the link between sleep and memory consolidation.

Weaknesses:

Some claims lack sufficient evidence or clarity:

(1) All sleep experiments are conducted under the "training" (temperature-change) condition. While genotypic controls are helpful, additional no-training controls are required to confirm that the observed differences are due to training rather than unknown genotype-related factors. The fact that experimental genotypes exhibit significantly altered sleep even before "training" (e.g., Figs. 7H, J, K, 8A, B, D) highlights the necessity of these controls.

(2) Previous studies on disrupted memory due to sleep reduction have primarily examined conditions with severe sleep deprivation. In contrast, this report claims that relatively small decreases in total sleep accompanied by sleep fragmentation are responsible for impaired memory consolidation. It remains unclear whether sleep fragmentation at this level is truly critical for memory consolidation. The authors should cause sleep loss and fragmentation of similar magnitude through other means and determine whether it can impair LTM.

(3) The authors employed a neural activity reporter to show that starvation increases the basal activity of PAM-a1 but not DPM neurons in untrained flies (Figures 9C-E). They observed small increases in the activity of both neuron groups immediately after training but not one hour later. Given the inhibitory connection from PAM-a1 to DPM, it is unclear why both neuron groups show increased activity after training. Additionally, as the authors acknowledge, it is puzzling how the inactivation of PAM-a1 produces similar effects on sleep and memory as DPM inhibition and PAM-a1 activation. Further experiments are needed to clarify these findings, such as manipulating PAM-a1 activity during the one-hour post-training period and evaluating the effect on DPM activity. Including data from training under fed conditions would provide a more comprehensive understanding of state-dependent neural activity. Even if certain experiments are not feasible, these issues warrant further discussion. It is also important to clarify that the term "synchronized" does not imply single-spike-level synchrony.

(4) The authors considered that PAM-a1 and DPM might function in parallel, independent pathways for sleep and LTM. They rejected this possibility based on the lack of additive effects when both neuronal groups were simultaneously inactivated. However, they found that MB299B-labelled neurons exert stronger memory effects than MB043B-labelled neurons, while MB043B neurons have stronger sleep effects. If sleep is a primary driver of memory consolidation, a stronger correlation between memory and sleep effects would be expected. This observation merits further discussion.

(5) Given prior knowledge that PAM neurons are heterogeneous and that the R58E02 driver is broadly expressed, data in Figures 1-5 concerning PAM are outdated. The use of more restricted PAM-a1 drivers from the outset would make the manuscript easier to read and interpret.

(6) Some figures lack relevant data, certain experiments are missing necessary controls, and anomalies are present in some data sets.

Reviewer #3 (Public review):

Summary:

Understanding the neural circuits that link sleep and memory remains a fundamental challenge in neuroscience. In this study, Lin Yan and colleagues investigate how dopamine signaling in Drosophila regulates long-term memory (LTM) formation in the context of sleep. They identify a specific microcircuit between protocerebral anterior medial dopamine neurons (PAM-DANs) and dorsal paired medial (GABAergic DPM) neurons that modulates memory consolidation. Their findings suggest that disrupting the basal activity of PAM-α1 neurons during early consolidation impairs LTM, with particularly pronounced effects under starvation conditions. Notably, sleep fragmentation caused by this disruption can be pharmacologically rescued, restoring LTM. These results provide compelling evidence that dopamine signaling plays a crucial role in linking sleep and memory, offering new insights into the underlying mechanisms.

Strengths:

This study presents a well-executed investigation into sleep-memory interactions, utilizing a combination of connectomics, behavioral assays, functional imaging, and pharmacological manipulations. The authors convincingly demonstrate that the PAM-α1 and DPM circuits interact, highlighting a potential mechanism by which sleep influences memory consolidation. The anatomical and functional dissection of this circuit is of high interest to the field, and the study's integration of sleep and memory processes contributes significantly to our understanding of dopamine's role in cognitive functions.

Weaknesses:

While the study is well-designed and presents compelling findings, some aspects require further clarification. The interpretation of dopamine receptor signaling remains incomplete, particularly regarding inhibitory pathways. The role of DPM in memory consolidation is not entirely conclusive, as different genetic approaches yield variable results. Additionally, some inconsistencies in neuronal activity patterns and experimental variability, especially regarding sleep patterns or pharmacological rescue, should be addressed to strengthen the mechanistic framework.

Conclusion:

Overall, this study provides valuable new insights into how sleep and dopamine circuits interact to regulate memory consolidation. While the findings are compelling, addressing the points above-particularly receptor signaling and the specific role of DPM and its activity patterns within the microcircuit would further solidify the study's conclusions.

eLife Assessment

Lu and colleagues developed an important imaging protocol that combines expansion microscopy, light-sheet microscopy, and image segmentation for use with the planarian Schmidtea mediterranea, a powerful model system for regeneration. This represents a substantial improvement on current standards and enables more rapid data acquisition. The utility of this solid protocol is demonstrated by quantifying several aspects of this flatworm's neural anatomy and musculature during homeostasis and regeneration. This work will be of interest to researchers looking to implement more systematic approaches towards imaging and quantifying intact specimens.

Reviewer #1 (Public review):

Summary:

The planarian flatworm Schmidtea mediterranea is widely used as a model system for regeneration because of its remarkable ability to regenerate its entire body plan from very small fragments of tissue, including the complete and rapid regeneration of the CNS. Prior to this study, analysis of CNS regeneration in planaria has mostly been performed on a gross anatomical level. Lu et al. describe a careful and detailed analysis of the planarian neuroanatomy and musculature in both the homeostatic and regenerating contexts. To improve the effective resolution of their imaging, the authors optimized a tissue expansion protocol for planaria. Imaging was performed by light sheet microscopy, and the resulting optical sections were tiled to reconstruct whole worms. Labelled tissues and cells were then segmented to allow quantification of neurons, muscle fibers, and all cells in individual worms.

Strengths:

The resulting workflow can produce highly detailed and quantifiable 3D reconstructions at a rate that is fast enough to allow the analysis of large numbers of whole animals.

Weaknesses:

While Lu et al. have shown how their methodology and workflow can be used to image and quantify features from whole animals, it is unclear how well their technique as described will perform at sub-cellular resolutions based upon the data that they show.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors apply tissue expansion and tiling light sheet microscopy to study allometric growth and regeneration in planaria. They developed image analysis pipelines to help them quantify different neuronal subtypes and muscles in planaria of different sizes and during regeneration. Among the strengths of this work, the authors provide beautiful images that show the potential of the approaches they are taking and their ability to quantify specific cell types in relatively large numbers of whole animal samples. Many of their findings confirm previous results in the literature, which helps validate the techniques and pipelines they have applied here. Among their new observations, they find that the body wall muscles at the anterior and posterior poles of the worm are organized differently and show that the muscle pattern in the posterior head of beta-catenin RNAi worms resembles the anterior muscle pattern. They also show that glial cell processes appear to be altered in beta-catenin or insulin receptor-1 RNAi worms. Weaknesses include some over-interpretation of the data and lack of consideration or citation of relevant previous literature, as discussed below.

Strengths:

This method of tissue expansion will be useful for researchers interested in studying this experimental animal. The authors provide high-quality images that show the utility of this technique. Their analysis pipeline permits them to quantify cell types in relatively large numbers of whole animal samples.

The authors provide convincing data on changes in total neurons and neuronal sub-types in different-sized planaria. They report differences in body wall muscle pattern between the anterior and posterior poles of the planaria, and that these differences are lost when a posterior head forms in beta-catenin RNAi planaria. They also find that glial cell projections are reduced in insulin receptor-1 RNAi planaria.

Comments on revisions:

The authors have satisfactorily addressed the major concerns of the previous reviewers.

Author response:

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

Reviewer #1(Public review):

comment 1: Lu et al. use their workflow to visualize RNA expression of five enzymes that are each involved in the biosynthetic pathway of different neurotransmitters/modulators, namely chat (cholinergeric), gad (GABAergic), tbh (octopaminergic), th (dopaminergic), and tph (serotonergic). In this way, they generate an anatomical atlas of neurons that produce these molecules. Collectively these markers are referred to as the "neuronpool." They overstate when they write, "The combination of these five types of neurons constitutes a neuron pool that enables the labeling of all neurons throughout the entire body." This statement does not accurately represent the state of our knowledge about the diversity of neurons in S. mediterranea. There are several lines of evidence that support the presence of glutamatergic and glycinergic neurons, including the following. The glutamate receptor agonists NMDA and AMPA both produce seizure-like behaviors in S. mediterranea that are blocked by the application of glutamate receptor antagonists MK-801 and DNQX (which antagonize NMDA and AMPA glutamate receptors, respectively; Rawls et al., 2009). scRNA-Seq data indicates that neurons in S. mediterranea express a vesicular glutamate transporter, a kainite-type glutamate receptor, a glycine receptor, and a glycine transporter (Brunet Avalos and Sprecher, 2021; Wyss et al., 2022). Two AMPA glutamate receptors, GluR1 and GluR2, are known to be expressed in the CNS of another planarian species, D. japonica (Cebria et al., 2002). Likewise, there is abundant evidence for the presence of peptidergic neurons in S. mediterranea (Collins et al., 2010; Fraguas et al., 2012; Ong et al., 2016; Wyss et al., 2022; among others) and in D. japonica (Shimoyama et al., 2016). For these reasons, the authors should not assume that all neurons can be assayed using the five markers that they selected. The situation is made more complex by the fact that many neurons in S. mediterranea appear to produce more than one neurotransmitter/modulator/peptide (Brunet Avalos and Sprecher, 2021; Wyss et al., 2022), which is common among animals (Vaaga et al., 2014; Brunet Avalos and Sprecher, 2021). However the published literature indicates that there are substantial populations of glutamatergic, glycinergic, and peptidergic neurons in S. mediterranea that do not produce other classes of neurotransmission molecule (Brunet Avalos and Sprecher, 2021; Wyss et al., 2022). Thus it seems likely that the neuronpool will miss many neurons that only produce glutamate, glycine or a neuropeptide.

In response to your comments, we agree that our initial statement regarding the "neuron pool" overstated the extent of neuronal coverage provided by the five selected markers. We have revised the sentence as “The combination of these five types of neurons constitutes a neuron pool that enables the labeling of most of the neurons throughout the entire body, including the eyes, brain, and pharynx”.

Furthermore, we chose the five neurotransmitter systems (cholinergic, GABAergic, octopaminergic, dopaminergic, and serotonergic) based on their well-characterized roles in planarian neurobiology and the availability of reliable markers. However, we acknowledge the limitations of this approach and recognize that it does not encompass all neuron types, particularly those involved in glutamatergic, glycinergic, and peptidergic signaling, which have been documented in S. mediterranea. We have also added the content about other neuron types in our revised results section “Additionally, the neuron system of S. mediterranea is complex which characterized by considerable diversity among glutamatergic, glycinergic, and peptidergic neurons in planarians and many neurons in S. mediterranea express more than one neurotransmitter or neuropeptide, which adds further complexity to the system. We used five markers for a proof of concept illustration. By employing Fluorescence in Situ Hybridization (FISH), we successfully visualized a variety of planarian neurons, including cholinergic (chat⁺), serotonergic (tph⁺), octopaminergic (tbh⁺), GABAergic (gad⁺), and dopaminergic (th⁺) neurons based on their well-characterized roles in planarian neurobiology and the availability of reliable markers. (Figure S2A, Supplemental video 2) (Currie et al., 2016). The combination of these five types of neurons constitutes a neuron pool that enables the labeling of most of the neurons throughout the entire body, including the eyes, brain, and pharynx (Figure 1B).”

comment 2: The authors use their technique to image the neural network of the CNS using antibodies raised vs. Arrestin, Synaptotagmin, and phospho-Ser/Thr. They document examples of both contralateral and ipsilateral projections from the eyes to the brain in the optic chiasma (Figure 1C-F). These data all seem to be drawn from a single animal in which there appears to be a greater than normal number of nerve fiber defasciculatations. It isn't clear how well their technique works for fibers that remain within a nerve tract or the brain. The markers used to image neural networks are broadly expressed, and it's possible that most nerve fibers are too densely packed (even after expansion) to allow for image segmentation. The authors also show a close association between estrella-positive glial cells and nerve fibers in the optic chiasma.

Thank you for your detailed feedback. While we did not perform segmentation of all neuron fibers, we were able to segment more isolated fibers that were not densely packed within the neural tracts. We use 120 nm resolution to segment neurons along the three axes. Our data show the presence of both contralateral and ipsilateral projections of visual neurons. Although Figure 1C-F shows data from one planarian, we imaged three independent specimens to confirm the consistency of these observations. In the revised manuscript, we have included a discussion on the limitations of TLSM in reconstructing neural networks. In the discussion part, we added “It should be noted that the current resolution for our segmentation may be limited when resolving fibers within densely packed regions of the nerve tracts”.

comment 3: The authors count all cell types, neuron pool neurons, and neurons of each class assayed. They find that the cell number to body volume ratio remains stable during homeostasis (Figure S3C), and that the brain volume steadily increases with increasing body volume (Figure S3E). They also observe that the proportion of neurons to total body cells is higher in worms 2-6 mm in length than in worms 7-9 mm in length (Figure 2D, S3F). They find that the rate at which four classes of neurons (GABAergic, octopaminergic, dopaminergic, serotonergic) increase relative to the total body cell number is constant (Figure S3G-J). They write: "Since the pattern of cholinergic neurons is the major cell population in the brain, these results suggest that the above observation of the non-linear dynamics between neurons and cell numbers is likely from the cholinergic neurons." This conclusion should not be reached without first directly counting the number of cholinergic neurons and total body cells. Given that glutamatergic, glycinergic, and peptidergic neurons were not counted, it also remains possible that the non-linear dynamics are due (in part or in whole) to one or more of these populations.

We have revised the statement into “These results suggest that the above observation of the non-linear dynamics between neuron and total cell number is not likely from the octopaminergic, GABAergic, dopaminergic, and serotonergic neurons. Since our neuron pool may not include glutamatergic, glycinergic, and peptidergic neurons, the non-linear dynamics may be from cholinergic neurons or other neurons not included in our staining.”

Reviewer #2 (Public review):

Weaknesses:

(1) The proprietary nature of the microscope, protected by a patent, limits the technical details provided, making the method hard to reproduce in other labs.

Thank you for your comment. We understand the importance of reproducibility and transparency in scientific research. We would like to point out that the detailed design and technical specifications of the TLSM are publicly available in our published work: Chen et al., Cell Reports, 2020. Additionally, the protocol for C-MAP, including the specific experimental steps, is comprehensively described in the methods section of this paper. We believe that these resources should provide sufficient information for other labs to replicate the method.

(2) The resolution of the analyses is mostly limited to the cellular level, which does not fully leverage the advantages of expansion microscopy. Previous applications of expansion microscopy have revealed finer nanostructures in the planarian nervous system (see Fan et al. Methods in Cell Biology 2021; Wang et al. eLife 2021). It is unclear whether the current protocol can achieve a comparable resolution.

Thank you for raising this important point. The strength of our C-MAP protocol lies in its fluorescence-protective nature and user convenience. Notably, the sample can be expanded up to 4.5-fold linearly without the need for heating or proteinase digestion, which helps preserve fluorescence signals. In addition, the entire expansion process can be completed within 48 hours. While our current analysis focused on cellular-level structures, our method can achieve comparable or better resolution and we will add this information in the revised manuscript as “It is important to point out that the strength of our C-MAP protocol lies in its fluorescence-protective nature and user convenience. Notably, the sample can be expanded up to 4.5-fold linearly without the need for heating or proteinase digestion, which helps preserve fluorescence signals. In addition, the entire expansion process can be completed within 48 hours. Based on our research requirement, two spatial resolutions were adopted to image expanded planarians, 2×2×5 μm³ and 0.5×0.5×1.6 μm³. The resolution can be further improved to 500 nm and 120 nm, respectively.”

(3) The data largely corroborate past observations, while the novel claims are insufficiently substantiated.

A few major issues with the claims:

Line 303-304: While 6G10 is a widely used antibody to label muscle fibers in the planarian, it doesn't uniformly mark all muscle types (Scimone at al. Nature 2017). For a more complete view of muscle fibers, it is important to use a combination of antibodies targeting different fiber types or a generic marker such as phalloidin. This raises fundamental concerns about all the conclusions drawn from Figures 4 and 6 about differences between various muscle types. Additionally, the authors should cite the original paper that developed the 6G10 antibody (Ross et al. BMC Developmental Biology 2015).

We appreciate the reviewer’s insightful comments and acknowledge that 6G10 does not uniformly label all muscle fiber types. We agree that this limitation should be recognized in the interpretation of our results. We have revised the manuscript to explicitly state the limitations of using 6G10 alone for muscle fiber labeling and highlight the need for additional markers. We have included the following statement in the Results section: “It is noted that previous studies reported that 6G10 does not label all body wall muscles equivalently with the limitation of predominantly labeling circular and diagonal fibers (Scimone et al., 2017; Ross et al., 2015). Our observation may be limited by this preference”. We would also clarify that the primary objective of our study was to demonstrate the application of our 3D tissue reconstruction method in addressing traditional research questions. Nonetheless, we agree that expanding the labeling strategy in future studies would allow for a more thorough investigation of muscle fiber diversity. Relevant citations have been properly revised and updated.

(4) Lines 371-379: The claim that DV muscles regenerate into longitudinal fibers lacks evidence. Furthermore, previous studies have shown that TFs specifying different muscle types (DV, circular, longitudinal, and intestinal) both during regeneration and homeostasis are completely different (Scimone et al., Nature 2017 and Scimone et al., Current Biology 2018). Single-cell RNAseq data further establishes the existence of divergent muscle progenitors giving rise to different muscle fibers. These observations directly contradict the authors' claim, which is only based on images of fixed samples at a coarse time resolution.

Thank you for your valuable feedback. Our intent was not to suggest that DV muscles regenerate into longitudinal fibers. Our observations focused on the wound site, where DV muscle fibers appear to reconnect, and longitudinal fibers, along with other muscle types, gradually regenerate to restore the structure of the injured area. We have revised the our statement as:“During the regeneration process, DV muscle fibers reconnect at the wound site, with longitudinal fibers and other muscle types gradually restoring the structure at the anterior tip and later integrating with circular and diagonal fibers through small DV fiber branches (Figure S5O1-O3).”

(5) Line 423: The manuscript lacks evidence to claim glia guide muscle fiber branching.

We agree with your concerns that our statement may be overestimated. We have removed this statement from the revised version. Instead, we focused on describing our observations of the connections between glial cells and muscle fibers. We have revised the section as follows: “Considering the interaction between glial and muscle cells, the localization of estrella⁺ glia and muscle fibers is further investigated. By dual-staining of anti-Phospho (Ser/Thr) and 6G10 in inr-1 RNAi and β-catenin-1 RNAi planarians, we found that the morphologies of neurons are normal, and they have close contact with muscle fibers (Figure 6D, E). However, by dual staining of estrella and 6G10, we found that the structure of glial cells is star-shaped in egfp RNAi planarian, however, glial cells in inr-1 RNAi and β-catenin-1 RNAi planarians have shorter cytoplasmic projections, and their sizes are smaller, lacking the major projection onto the muscles (Figure 6D, E, Figure S6E-K). Especially, in the posterior head of β-catenin-1 RNAi planarians, the glial cell has few axons and can hardly connect with muscle fibers (Figure 6E). These results indicated that proper neuronal guidance and muscle fiber distribution could potentially contribute to facilitating accurate glial-to-muscle projections.

(6) Lines 432/478: The conclusion about neuronal and muscle guidance on glial projections is similarly speculative, lacking functional evidence. It is possible that the morphological defects of estrella+ cells after bcat1 RNAi are caused by Wnt signaling directly acting on estrella+ cells independent of muscles or neurons.

We understand that this approach is insufficient and we have revised the this section as follows: “Further investigation is required to distinguish the cell-autonomous and non-autonomous effects of inr-1 RNAi and β-catenin-1 RNAi on muscle and glial cells.”

(7) Finally, several technical issues make the results difficult to interpret. For example, in line 125, cell boundaries appear to be determined using nucleus images; in line 136, the current resolution seems insufficient to reliably trace neural connections, at least based on the images presented.

We use two setups for imaging cells and neuron projections. For cellular resolution imaging, we utilized a 1× air objective with a numerical aperture (NA) of 0.25 and a working distance of 60 mm (OLYMPUS MV PLAPO). The voxel size used was 0.8×0.8×2.5 μm³. This configuration resulted in a resolution of 2×2×5 μm³ and a spatial resolution of 0.5×0.5×1.25 μm³ with 4.5× isotropic expansion. Alternatively, for sub-cellular imaging, we employed a 10×0.6 SV MP water immersion objective with 0.8 NA and a working distance of 8 mm (OLYMPUS). The voxel size used in this configuration was 0.26×0.26×0.8 μm³. As a result of this configuration, we achieved a resolution of 0.5×0.5×1.6 μm³ and a spatial resolution of 0.12×0.12×0.4 μm³ with a 4.5× isotropic expansion. The higher resolution achieved with sub-cellular imaging allows us to observe finer structures and trace neural connections.

Regarding your question about cell boundaries, we have revised the manuscript to specify that the boundaries we identified are those of each nucleus.

Reviewer #3 (Public review):

Weaknesses:

(1) The work would have been strengthened by a more careful consideration of previous literature. Many papers directly relevant to this work were not cited. Such omissions do the authors a disservice because in some cases, they fail to consider relevant information that impacts the choice of reagents they have used or the conclusions they are drawing.

For example, when describing the antibody they use to label muscles (monoclonal 6G10), they do not cite the paper that generated this reagent (Ross et al PMCID: PMC4307677), and instead, one of the papers they do cite (Cebria 2016) that does not mention this antibody. Ross et al reported that 6G10 does not label all body wall muscles equivalently, but rather "predominantly labels circular and diagonal fibers" (which is apparent in Figure S5A-D of the manuscript being reviewed here). For this reason, the authors of the paper showing different body wall muscle populations play different roles in body patterning (Scimone et al 2017, PMCID: PMC6263039, also not cited in this paper) used this monoclonal in combination with a polyclonal antibody to label all body wall muscle types. Because their "pan-muscle" reagent does not label all muscle types equivalently, it calls into question their quantification of the different body wall muscle populations throughout the manuscript. It does not help matters that their initial description of the body wall muscle types fails to mention the layer of thin (inner) longitudinal muscles between the circular and diagonal muscles (Cebria 2016 and citations therein).

Ipsilateral and contralateral projections of the visual axons were beautifully shown by dye-tracing experiments (Okamoto et al 2005, PMID: 15930826). This paper should be cited when the authors report that they are corroborating the existence of ipsilateral and contralateral projections.

Thank you for your feedback. We have incorporated these citations and clarifications into the revised manuscript. We acknowledge the limitations of this approach and have added a statement for this limitation in the revised manuscript “It is noted that previous studies reported that 6G10 does not label all body wall muscles equivalently with the limitation of predominantly labeling circular and diagonal fibers (Scimone et al., 2017; Ross et al., 2015). Our observation may be limited by this preference.”

(2) The proportional decrease of neurons with growth in S. mediterranea was shown by counting different cell types in macerated planarians (Baguna and Romero, 1981; https://link.springer.com/article/10.1007/BF00026179) and earlier histological observations cited there. These results have also been validated by single-cell sequencing (Emili et al, bioRxiv 2023, https://www.biorxiv.org/content/10.1101/2023.11.01.565140v). Allometric growth of the planaria tail (the tail is proportionately longer in large vs small planaria) can explain this decrease in animal size. The authors never really discuss allometric growth in a way that would help readers unfamiliar with the system understand this.

Thank you for your feedback. We have incorporated these citations and clarifications into the revised manuscript “These findings provide evidence to support the previous prediction and consistency between different planarian species (Baguñà et al., 1981; Emili et al.,2023). Because the tail is proportionately longer in large than in small planarians, the allometric growth of the planarians can be one possibility for this decrease along with the increase in animal size. The phenomenon may also suggest the existence of a threshold in the increase of planarian neuron numbers, which may ultimately contribute to some physiological changes, such as planarian fission.”

(3) In some cases, the authors draw stronger conclusions than their results warrant. The authors claim that they are showing glial-muscle interactions, however, they do not provide any images of triple-stained samples labeling muscle, neurons, and glia, so it is impossible for the reader to judge whether the glial cells are interacting directly with body wall muscles or instead with the well-described submuscular nerve plexus. Their conclusion that neurons are unaffected by beta-cat or inr-1 RNAi based on anti-phospho-Ser/Thr staining (Fig. 6E) is unconvincing. They claim that during regeneration "DV muscles initially regenerate into longitudinal fibers at the anterior tip" (line 373). They provide no evidence for such switching of muscle cell types, so it is unclear why they say this.

We acknowledge that some of our conclusions were overclaimed given the current data, and we appreciate the opportunity to clarify and refine these claims in the revised manuscript. Due the technique reason, we have not achieved the triple-staining to address this concern. We hope to make a progress in our future studies. Regarding the statement that "DV muscles initially regenerate into longitudinal fibers at the anterior tip" (line 373), as addressed in our previous response, this statement was unclear. Our intent was not to imply that DV muscles switch into longitudinal fibers. Instead, we observed that muscle fibers reconnect at the wound site, with longitudinal fibers and other muscle types gradually restoring the structure. We have revised this section: “During the regeneration process, DV muscle fibers reconnect at the wound site, with longitudinal fibers and other muscle types gradually restoring the structure at the anterior tip and later integrating with circular and diagonal fibers through small DV fiber branches (Figure S5O1-O3).”

(4) The authors show how their automated workflow compares to manual counts using PI-stained specimens (Figure S1T). I may have missed it, but I do not recall seeing a similar ground truth comparison for their muscle fiber counting workflow. I mention this because the segmented image of the posterior muscles in Figure 4I seems to be missing the vast majority of circular fibers visible to the naked eye in the original image.

Thank you for raising this important point. We have included a ground truth comparison of our automated muscle fiber segmentation with the original image in the revised Figure S6. The original Figure S6 has been changed as Figure S7. Regarding the observation of missing circular fibers in Figure 4I, we agree that the segmentation appears to have missed a significant number of circular fibers in this particular image. This may have been due to limitations in the current parameters of the segmentation algorithm, especially in distinguishing fibers in regions of varying intensity or overlap.

(5) It is unclear why the abstract says, "We found the rate of neuron cell proliferation tends to lag..." (line 25). The authors did not measure proliferation in this work and neurons do not proliferate in planaria.

Thank you for pointing out this mistake. What we intended to convey was the increase in neuron number during homeostasis. We have revised the abstract “We found that the increase in neuron cell number tends to lag behind the rapid expansion of somatic cells during the later phase of homeostasis.”

(6) It is unclear what readers are to make of the measurements of brain lobe angles. Why is this a useful measurement and what does it tell us?

The measurement of brain lobe angles is intended to provide a quantitative assessment of the growth and morphological changes of the planarian brain during regeneration. Additionally, the relevance of brain lobe angles has been explored in previous studies, such as Arnold et al., Nature, 2016, further supporting its use as a meaningful parameter.

(7) The authors repeatedly say that this work lets them investigate planarians at the single-cell level, but they don't really make the case that they are seeing things that haven't already been described at the single-cell level using standard confocal microscopy.

Thank you for your comment. We agree that single-cell level imaging has been previously achieved in planarians using conventional confocal microscopy. However, our goal was to extend the application of expansion microscopy by combining C-MAP with tiling light sheet microscopy (TLSM), which allows for faster and high-resolution 3D imaging of whole-mount planarians. We have added in the discussion section: “This combination offers several key advantages over standard techniques. For example, it enables high-throughput imaging across entire organisms with a level of detail and speed that is not easily achieved using confocal methods. This approach allows us to investigate the planarian nervous system at multiple developmental and regenerative stages in a more comprehensive manner, capturing large-scale structures while preserving fine cellular details. The ability to rapidly image whole planarians in 3D with this resolution provides a more efficient workflow for studying complex biological processes.”

eLife Assessment

This study makes the fundamental discovery of the first natural animal rhodopsin that uses a chloride ion instead of an amino acid side chain as a counterion. Using a combination of biochemical and spectroscopic experiments together with QM/MM simulations, the authors identify the spectral tuning mechanism in the dark state and in the photoproduct state. The methods are sound and the results are convincing. This work will be of interest to biologists working on visual proteins and it also raises new questions about how environmental factors might affect coral opsins.

Reviewer #1 (Public review):

The chromophore molecule of animal and microbial rhodopsins is retinal which forms a Schiff base linkage with a lysine in the 7-th transmembrane helix. In most cases, the chromophore is positively charged by protonation of the Schiff base, which is stabilized by a negatively charged counterion. In animal opsins, three sites have been experimentally identified, Glu94 in helix 2, Glu113 in helix 3, and Glu181 in extracellular loop 2, where a glutamate acts as the counterion by deprotonation. In this paper, Sakai et al. investigated molecular properties of anthozoan-specific opsin II (ASO-II opsins), as they lack these glutamates. They found an alternative candidate, Glu292 in helix 7, from the sequences. Interestingly, the experimental data suggested that Glu292 is not the direct counterion in ASO-II opsins. Instead, they found that ASO-II opsins employ a chloride ion as the counterion. In the case of microbial rhodopsin, a chloride ion serves as the counterion of light-driven chloride pumps. This paper reports the first observation of a chloride ion as the counterion in animal rhodopsin. Theoretical calculation using a QM/MM method supports their experimental data. The authors also revealed the role of Glu292, which serves as the counterion in the photoproduct, and is involved in G protein activation.

The conclusions of this paper are well supported by data, while the following aspects should be considered for the improvement of the manuscript.

(1) Information on sequence alignment only appears in Figure S2, not in the main figures. Figure S2 is too complicated by so many opsins and residue positions. It will be difficult for general readers to follow the manuscript because of such an organization. I recommend the authors show key residues in Figure 1 by picking up from Figure S2.

(2) Halide size dependence. The authors observed spectral red-shift for larger halides. Their observation is fully coincident with the chromophore molecule in solution (Blatz et al. Biochemistry 1972), though the isomeric states are different (11-cis vs all-trans). This suggests that a halide ion is the hydrogen-bonding acceptor of the Schiff base N-H group in solution and ASO-II opsins. A halide ion is not the hydrogen-bonding acceptor in the structure of halorhodopsin, whose halide size dependence is not clearly correlated with absorption maxima (Scharf and Engelhard, Biochemistry 1994). These results support their model structure (Figure 4), and help QM/MM calculations.

(3) QM/MM calculations. According to Materials and Methods, the authors added water molecules to the structure and performed their calculations. However, Figure 4 does not include such water molecules, and no information was given in the manuscript. In addition, no information was given for the chloride binding site (contact residues) in Figure 4. More detailed information should be shown with additional figures in Figure SX.

(4) Figure 5 clearly shows much lower activity of E292A than that of WT, whose expression levels are unclear. How did the authors normalize (or not normalize) expression levels in this experiment?

(5) The authors propose the counterion switching from a chloride ion to E292 upon light activation. A schematic drawing on the chromophore, a chloride ion, and E292 (and possible surroundings) in Antho2a and the photoproduct will aid readers' understanding.

Reviewer #2 (Public review):

Summary:

This work reports the discovery of a new rhodopsin from reef-building corals that is characterized experimentally, spectroscopically, and by simulation. This rhodopsin lacks a carboxylate-based counterion, which is typical for this family of proteins. Instead, the authors find that a chloride ion stabilizes the protonated Schiff base and thus serves as a counterion.

Strengths:

This work focuses on the rhodopsin Antho2a, which absorbs in the visible spectrum with a maximum at 503 nm. Spectroscopic studies under different pH conditions, including the mutant E292A and different chloride concentrations, indicate that chloride acts as a counterion in the dark. In the photoproduct, however, the counterion is identified as E292.

These results lead to a computational model of Antho2a in which the chloride is modeled in addition to the Schiff base. This model is improved using the hybrid QM/MM simulations. As a validation, the absorption maximum is calculated using the QM/MM approach for the protonated and deprotonated E292 residue as well as the E292A mutant. The results are in good agreement with the experiment. However, there is a larger deviation for ADC(2) than for sTD-DFT. Nevertheless, the trend is robust since the wt and E292A mutant models have similar excitation energies. The calculations are performed at a high level of theory that includes a large QM region.

Weaknesses:

I have a couple of questions about this study:

(1) I find it suspicious that the absorption maximum is so close to that of rhodopsin when the counterion is very different. Is it possible that the chloride creates an environment for the deprotonated E292, which is the actual counterion?

(2) The computational protocol states that water molecules have been added to the predicted protein structure. Are there water molecules next to the Schiff base, E292, and Cl-? If so, where are they located in the QM region?

(3) If the E292 residue is the counterion in the photoproduct state, I would expect the retinal Schiff base to rotate toward this side chain upon isomerization. Can this be modeled based on the recent XFEL results on rhodopsin?

Reviewer #3 (Public review):

Summary:

The paper by Saito et al. studies the properties of anthozoan-specific opsins (ASO-II) from organisms found in reef-building coral. Their goal was to test if ASO-II opsins can absorb visible light, and if so, what the key factors involved are.

The most exciting aspect of this work is their discovery that ASO-II opsins do not have a counterion residue (Asp or Glu) located at any of the previously known sites found in other animal opsins.

This is very surprising. Opsins are only able to absorb visible (long wavelength light) if the retinal Schiff base is protonated, and the latter requires (as the name implies) a "counter ion". However, the authors clearly show that some ASO-II opsins do absorb visible light.

To address this conundrum, they tested if the counterion could be provided by exogenous chloride ions (Cl-). Their results find compelling evidence supporting this idea, and their studies of ASO-II mutant E292A suggest E292 also plays a role in G protein activation and is a counterion for a protonated Schiff base in the light-activated form.

Strengths:

Overall, the methods are well-described and carefully executed, and the results are very compelling.

Their analysis of seven ASO-II opsin sequences undoubtedly shows they all lack a Glu or Asp residue at "normal" (previously established) counter-ion sites in mammalian opsins (typically found at positions 94, 113, or 181). The experimental studies clearly demonstrate the necessity of Cl- for visible light absorbance, as do their studies of the effect of altering the pH.

Importantly, the authors also carried out careful QM/MM computational analysis (and corresponding calculation of the expected absorbance effects), thus providing compelling support for the Cl- acting directly as a counterion to the protonated retinal Schiff base, and thus limiting the possibility that the Cl- is simply altering the absorbance of ASO-II opsins through some indirect effect on the protein.

Altogether, the authors achieved their aims, and the results support their conclusions. The manuscript is carefully written, and refreshingly, the results and conclusions are not overstated.

This study is impactful for several reasons. There is increasing interest in optogenetic tools, especially those that leverage G protein-coupled receptor systems. Thus, the authors' demonstration that ASO-II opsins could be useful for such studies is of interest.

Moreover, the finding that visible light absorbance by an opsin does not absolutely require a negatively charged amino acid to be placed at one of the expected sites (94, 113, or 181) typically found in animal opsins is very intriguing and will help future protein engineering efforts. The argument that the Cl- counterion system they discover here might have been a preliminary step in the evolution of amino acid based counterions used in animal opsins is also interesting.

Finally, given the ongoing degradation of coral reefs worldwide, the focus on these curious opsins is very timely, as is the authors' proposal that the lower Schiff base pKa they discovered here for ASO-II opsins may cause them to change their spectral sensitivity and G protein activation due to changes in their environmental pH.

eLife Assessment

This paper reports the analysis of coevolutionary patterns and dynamical information for identifying functionally relevant sites. These findings are considered important due to the broad utility of the unified framework and network analysis capable of revealing communities of key residues that go beyond the residue-pair concept. The data are solid and the results are clearly presented.

Reviewer #1 (Public review):

Summary:

As reported above, this paper by Xu et al reports on a new method to combine the analysis of coevolutionary patterns with dynamic profiles to identify functionally important residues and reveal correlations between binding sites.

Strengths:

In general, coevolutionary analysis and MD analysis are carried out separately and while there have been attempts to compare the information provided by the two, no unified framework exists. Here, the authors convincingly demonstrate that integrating signals from Dynamics and coevolution gives information that substantially overcomes the one provided by either method in isolation. While other methods are useful, they do not capture how dynamics is fundamental to define function and thus sculpts coevolution, via the 3D structure of the protein. At the same time, the authors demonstrate how coevolution in turn also influences internal dynamics. The Networks they rebuild unveil information at an even higher level: the model starts pairwise but through network representation the authors arrive to community analysis, reporting on interaction patterns that are larger than simple couples.

Comments on latest version:

I have nothing to add to this revision. The paper looks excellent and very interesting.

Reviewer #2 (Public review):

Summary:

The authors introduced a computational framework, DyNoPy, that integrates residue coevolution analysis with molecular dynamics (MD) simulations to identify functionally important residues in proteins. DyNoPy identifies key residues and residue-residue coupling to generate an interaction graph and attempts to validate using two clinically relevant β-lactamases (SHV-1 and PDC-3).

Strengths:

DyNoPy could not only show clinically relevance of mutations but also predict new potential evolutionary mutations. Authors have provided biologically relevant insights into protein dynamics which can have potential applications in drug discovery and understanding molecular evolution.

Comments on latest version:

I appreciate the efforts of the authors to address my comments.

Reviewer #3 (Public review):

Summary:

In this paper, Xu, Dantu and coworkers report a protocol for analyzing coevolutionary and dynamical information to identify a subset of communities that capture functionally relevant sites in beta-lactamases.

Strengths:

The combination of coevolutionary information and metrics from MD simulations is interesting for capturing functionally relevant sites, which can have implications in the fields of drug discovery but also in protein design.

Comments on latest version:

The authors have successfully addressed all my previous comments/concerns. I am happy with the current version of the manuscript.

Author response:

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

Reviewer #1 (Public review):

Summary:

As reported above, this paper by Xu et al reports on a new method to combine the analysis of coevolutionary patterns with dynamic profiles to identify functionally important residues and reveal correlations between binding sites.

Strengths:

In general, coevolutionary analysis and MD analysis are carried out separately and while there have been attempts to compare the information provided by the two, no unified framework exists. Here, the authors convincingly demonstrate that integrating signals from Dynamics and coevolution gives information that substantially overcomes the one provided by either method in isolation. While other methods are useful, they do not capture how dynamics is fundamental to define function and thus sculpts coevolution, via the 3D structure of the protein. At the same time, the authors demonstrate how coevolution in turn also influences internal dynamics. The Networks they rebuild unveil information at an even higher level: the model starts pairwise but through network representation the authors arrive to community analysis, reporting on interaction patterns that are larger than simple couples.

Weaknesses:

The authors should

- Make an effort in suggesting/commenting the limits of applicability of their method;

We have added a sentence on Page 17, line 15 that describes the limitation of our method.

- Expand discussion on how DyNoPy compares to other methods;

A paragraph has been added to explain the comparison with other models (Page 3, line 18)

- Dynamic is not essential in all systems (structural proteins): The authors may want to comment on possible strategies they would use for other systems where their framework may not be suitable/applicable.

We agree with the reviewer that dynamics is not essential in all systems. In systems where there is limited role of dynamics in the function, the analysis done with DyNoPy is equivalent to conventional coevolution analysis, which can be consider one limitation of our method. Conversely, for dynamic proteins, combining functional dynamics descriptors with coevolution analysis using DyNoPy, helps in denoising information by deconvolution of communities. We have included this in the manuscript to highlight the suitability/applicability of the method.

Further, we have added a paragraph in the Introduction and conclusions highlighting the main difference between DyNoPy and existing computational tools like DCCM, KIN, and SPM and for your convenience it is provided below:

“Functional sites are often regulated by both, local and global interactions. Changes in these interactions are instrumental for functional events like substrate binding, catalysis, and conformational changes (18). The development of physical models of protein dynamics and the increase in available computational power has stimulated the adoption of computational techniques (19, 20) to investigate the conformational dynamics of proteins, an essential component of the many biological functions (21, 22). Different models have been proposed to describe the interactions between residues during simulations and network models have been particularly popular,  including methods on single structures and MD simulations data built by analysing the response to external forces on residue networks (23), by estimating the prevalence of non-covalent energy interaction networks in homologous proteins (24), or by analysing linear or non-linear correlation in atomic fluctuations (25, 26). These techniques have demonstrated their usefulness in extracting allosteric networks from structural data with applications in enzyme design (26).”

Reviewer #2 (Public review):

Summary:

Authors introduced a computational framework, DyNoPy, that integrates residue coevolution analysis with molecular dynamics (MD) simulations to identify functionally important residues in proteins. DyNoPy identifies key residues and residue-residue coupling to generate an interaction graph and attempts to validate using two clinically relevant β-lactamases (SHV-1 and PDC-3).

Strengths:

DyNoPy could not only show clinically relevance of mutations but also predict new potential evolutionary mutations. Authors have provided biologically relevant insights into protein dynamics which can have potential applications in drug discovery and understanding molecular evolution.

Weaknesses:

Although DyNoPy could show the relevance of key residues in active and non-active site residues, no experiments have been performed to validate their predictions.

We thank the reviewer for highlighting this point. We acknowledge that direct experimental validation of our predictions for DyNoPy has not yet been performed. However, we have provided explanations and evidence from experiments conducted on closely related homologs to support the relevance of key residues. These homologs share significant structural and functional similarity, which strengthens the reliability of our predictions.

In addition, they should compare their method with conventional techniques and show how their method could be different.

We thank all the reviewers for highlighting this oversight on our behalf. In Introduction and conclusion, we have added the following paragraphs:

“Functional sites are often regulated by both, local and global interactions. Changes in these interactions are instrumental for functional events like substrate binding, catalysis, and conformational changes (18). The development of physical models of protein dynamics and the increase in available computational power has stimulated the adoption of computational techniques (19, 20) to investigate the conformational dynamics of proteins, an essential component of the many biological functions (21, 22). Different models have been proposed to describe the interactions between residues during simulations and network models have been particularly popular,  including methods on single structures and MD simulations data built by analysing the response to external forces on residue networks (23), by estimating the prevalence of non-covalent energy interaction networks in homologous proteins (24), or by analysing linear or non-linear correlation in atomic fluctuations (25, 26). These techniques have demonstrated their usefulness in extracting allosteric networks from structural data with applications in enzyme design (26). ”

An explanation of "communities" divided in the work and how these communities are relevant to the article should be provided. In addition, choice of collective variables and their relevance in residue coupling movement is also not very well explained. Dynamics cross correlation map can also be a good method for understanding the residue movements and can explain the residue-residue coupling, it is not explained how DyNoPy is different from the conventional methods or can perform better.

The following sentences have been included in the manuscript to address the questions raised by the reviewer:

On Community Definition and relevance

DyNoPy identified coevolving residue pairs (scaled coevolution score >1) with interactions strongly correlated with protein functional motions (i.e., J values larger than zero). Applying network analysis on the combined dynamics-coevolution matrix helps us extracting higher-order interactions beyond pairwise coupling and detecting critical residues, which show multiple interactions with each other. Moreover, indirect long-range relationships, which would be hard to identify from numerical data, could be detected through community clustering. Community-based analysis offers a more comprehensive understanding of residue relationships and enables the visualization of residue couplings on the protein structure.

On Choice of collective variables:

DyNoPy works on the assumption that time-dependent interactions between critical residues, either having significant structural change or not will correlate with functional conformational motions. Since MD simulation data is high-dimensional, a time-dependent dynamic descriptor is required to extract the most relevant information for the process under study. A good collective variable (CV) should appropriately describe protein functional motions. Thus, a CV that detects the highest number of residue couplings is expected to be the most suitable descriptor (Mentioned in Page 22 Line 14). In our study, we tested 12 CVs, either focusing on the entire protein or on selected regions. And the best performed CV (the one identified the most residue couplings) was selected for further analysis. In practical applications, users can decide whether to focus on the most relevant global or local dynamics descriptor  depending on the dynamics of their specific system.

We have added a paragraph in the Introduction differentiating DyNoPy with other methods including DCCM. DCCM differs from DyNoPy in two aspects 1) it does not account for inter-residue coevolution 2) the correlation matrix captures correlations of atomic/residue movements associated with the whole intrinsic dynamics of the system, without filtering for the contributions to the important motions involved in the biological function. Additionally, any residue pair contributing to functional motion without itself undergoing any structural change will not be visible in this approach.

In the sentence "DyNoPy identified eight significant communities of strongly coupled residues within SHV-1 (Supporting Fig. S4A)" I could not find a clear description of eight significant communities.

The following sentences have been included in the results, methods and figure legends that define ‘significant community’:

‘DyNoPy identified eight meaningful communities, each consisting of at least three strongly coupled residues within SHV-1 (Supplementary Fig. S4A). All crucial catalytic residues and critical substitution sites previously mentioned participating in one of these communities with the exceptions of R₄₃, R₂₀₂, and S₁₃₀.’ (Page 8 Line 28)

‘A meaningful community should contain at least three residues.’ (Page 21 Line 2)

‘A reasonable residue community should contain at least three residues.’ (SI Page 11)

Again the description of communities is not clear to me in the following sentence "Detailed description of the other three communities is provided in the supporting information (Fig. S6)."

This following sentence has been rewritten.

‘Detailed description of communities with secondary importance for protein function (community 3, 8, and 9) is provided in the supplementary information (Supplementary Fig. S6).’ (Page 9, line 8)

In the sentence "N170 acts as an intermediary between N136 and E166". Kindly cite the reference figure to show N179 as intermediate residue.

This sentence has been rewritten to avoid any confusion.

‘Although DyNoPy did not detect this direct interaction between N136 and E166, the established relationship between N136 and N170 highlights the role of N136 in influencing E166.’ (Page 10 Line 8)

Please be careful with the numbers. In the sentence "These residues not only interact with each other directly but are also indirectly coupled via 21 other residues." I could count 22 other residues and not 21.

We thank the reviewer for spotting this error. This has now been corrected. All the communities are counted again.

‘These residues not only interact with each other directly but are also indirectly coupled via 22 other residues.’ (Page 12 Line 14)

In the sentence "Unlike other substitution sites that are adjacent to the active site, R₂₀₅ is situated more than 16 Å away from catalytic serine S₇₀". Please add this label somewhere in the figure.

The figure legends have been updated to include this. Distances have been added to community 4 Fig. 3 and community 6 Fig. 4. Residue index in the legend of Fig.3 has been included as subscript. Distance in the main text has been changed to be more accurate.

‘G₁₅₆ and A₁₄₆ are two functional important residues distant from the active site. G₁₅₆ is 21.3Å away from the catalytic S₇₀. A₁₄₆ is 16.8Å away from S₇₀.’ (Page 12 Line 2)

‘R₂₀₅ is a functional important residue that is 20.6Å away from the active site S₇₀.’ (Page 13 Line 10)

Please cite a reference in the sentence "This indicates that mutations on G238 would result in an alteration on protein catalytic function, as well as an increased flexibility of the protein, which strongly aligns with previous finding."

The citation has been added

‘This indicates that mutations on G238 would result in an alteration on protein catalytic function, as well as an increased flexibility of the protein, which strongly aligns with previous finding (62).’ (Page 15 Line 2)

Reviewer #3 (Public review):

Summary:

In this paper, Xu, Dantu and coworkers report a protocol for analyzing coevolutionary and dynamical information to identify a subset of communities that capture functionally relevant sites in beta-lactamases.

Strengths:

The combination of coevolutionary information and metrics from MD simulations is interesting for capturing functionally relevant sites, which can have implications in the fields of drug discovery but also in protein design.

Weaknesses:

The combination of coevolutionary information and metrics from MD simulations is not new as other protocols have been proposed along the years (the current version of the paper neglects some of them, see below), and there are a few parameters of the protocol that, in my opinion, should be better analyzed and discussed.

(1) As mentioned, the introduction of the paper lacks some important publications in the field of using graph theory to represent important interaction networks extracted from MD simulations (DOI: 10.1002/pro.4911), and also combining MD data with MSA to identify functionally relevant sites for enzyme design (doi: 10.1021/acscatal.4c04587, 10.1093/protein/gzae005).

We are very grateful for pointing us to these references. We have added a paragraph in the Introduction mentioning these and other computational tools similar to DyNoPy. Further, in conclusion we have highlighted the differences between DyNoPy and existing tools.

(2) The matrix used to apply graph theory (J_ij) is built from summing the scaled coevolution and degree of correlation values. The alpha and beta weights are defined, and the authors mention that alpha is set to 0.5, thus beta as well to fulfil with the alpha + beta = 1. Why a value of 0.5 has been selected? How this affects the overall results and conclusions extracted? The finding that many catalytically relevant residues are identified in the communities is not surprising given that such sites usually present a high conservation score.

This is an excellent question. Our present formulation allows the user to easily assess the influence of coevolution and dynamic couplings on the output. Setting alpha to 0.5, weights both evolutionary and dynamics information equally and has shown promising results in SHV-1 and PDC-3. As it has been presented in the manuscript, setting alpha to 1, i.e., purely utilising coevolution data does not let us identify critical residues effectively as all residues are included in the set (Supplementary Fig. S4 and S5). In future work, we would like to investigate the effect of scanning alpha from 0 to 1 on the final residue list, possibly on a larger set of proteins and protein families.

We would also like to point out that some of the residue pairs with coevolution scores in the top 1% have J-scores set to 0, as they lacked significant coupling to the functional dynamics.

(3) Another important point that needs further explanation is the selection of the relevant descriptor of protein dynamics. In this study two different strategies have been used (one more global the other more local), but more details should be provided regarding their choice. What is the best strategy according to the authors? Why not using the same strategy for both related systems? The obtained results using one methodology or the other will have a large impact on the dynamical score. Another related point is: what is the impact of the MD simulation length, how the MSA is generated and number of sequences used for MSA construction?

As in the case of many complex proteins, the flow of information occurs in β-lactamases via structural interactions (https://doi.org/10.7554/eLife.66567). These interactions occur both on a local level, as in the case of binding site residues or residues immediately surrounding the binding site; however, there are interactions far away (>20Å) from the binding site that have the ability to alter function. We have obtained this information from extensive surveys of clinical isolates and experimental data. To account for such interactions, a more global approach has to be taken. To answer the reviewer’s question: each system is unique and there is no one-fixed strategy. In short, the method used should be able to denoise information and the user is advised to fine-tune their findings by corroborating with experimental and clinical information.

The length of MD simulations is also system specific. Some systems effectively sample the functional dynamics within a shorter simulation time, while others take a long timescale MD simulation to converge. The results won’t change as long as the simulation has effectively sampled the functional dynamics associated with biological function.

The MSA is generated by the HH-Suite package as mentioned on Page 19 Line 19. More specifically, the MSA is constructed based on the UniRef30 database, where sequences are clustered, and each cluster contains sequences with at least 30% sequence identity. This provides a non-redundant set of protein sequences. Our package allows the automatic generation of MSAs from the database. For SHV-1, the alignment contains 18,175 protein sequences and for PDC-3, the alignment consists of 27,892 protein sequences. Full details of this protocol are published in Bibik et al. (https://doi.org/10.1093/bioinformatics/btae166). We have revised the methods section to include these details.

Other Minor Alterations

‘Fig. S1 and S2’ has been changed to ‘Supplementary Fig. S1 and S2’ for consistency (Page 6 Line 12)

(1) ‘Figure 5B’ has been changed to ‘Fig. 5B’ for consistency (Page 16 Line 11)

(2) All the ‘Figure’ has been changed to ‘Fig.’ in the SI for consistency

(3) Just as the suggestion, an alteration has been made on the Step 1 of Fig.1.

eLife Assessment

CellDetective is a useful software package for segmentation, tracking, and analysis of time‐lapse microscopy datasets, specifically designed to be accessible to researchers without coding expertise. The authors provide solid evidence of its capabilities through comprehensive validations and well‐executed comparisons across immunological assays. However, the current implementation is limited to 2D widefield imaging and presents technical challenges - including occasional crashes, restricted flexibility in defining multiple cell populations, and some interface issues that hinder the full user experience. Overall, this work will be of significant interest to the bioimaging community, especially those in immunology and cell biology, and promises to evolve into a more robust tool with further development.

Reviewer #1 (Public review):

Summary:

In this manuscript, Torro et al. presented CellDetective, an open-source software designed for a user-friendly execution of single-cell segmentation, tracking, and analysis of time-lapse microscopy data. The authors demonstrated the applications of the software by measuring NK cell spreading events acquired with reflection interference contrast microscopy (RICM), as well as detecting target cell death events and their interaction with neighboring NK cells in a multichannel widefield microscopy dataset.

Strengths:

The segmentation (StarDist, Cellpose) and tracking (bTrack) modules implemented were based on existing and published software packages. The authors added the event detection, classification, and analysis modules to enable an end-to-end time-lapse microscopy data processing and analysis pipeline, complete with a graphical user interface (GUI). This minimizes the coding experience required from the user. The documentation that accompanies CellDetective is also adequate.

Weaknesses:

Given that the software was designed to improve user experience, such an approach also limits its scope and functionality and is currently capable of handling very specific types of experiments. Additionally, this reviewer has also encountered many technical difficulties (see documented bugs/crashes below) that have prevented an extensive exploration of all the functionality of CellDetective.

Specifics:

(1) The software can only handle 2D 'widefield' time-lapse imaging datasets. It should be noted that many studies that examine cell-cell interactions in vitro also used confocal microscopy and acquired the time-lapse images in 3D z-stacks to enable the reconstruction of entire cell volumes from multiple optical sections along the z-axis.

Given that almost all of the implemented segmentation (StarDist, Cellpose) and tracking (bTrack) packages already support the handling of 3D datasets, it is unclear why CellDetective was designed to only work with 2D datasets.

As noted above, extending the support for 3D images would allow the scope and utility of this software to be further extended for imaging studies acquired in z-stacks. As an example, the dense clustering of effector cells in Figure 4 had prevented accurate segmentation due to the 2D nature of the experimental dataset. More importantly, support for a 3D dataset could also allow for the tracking of fluorescent protein-based sub-cellular as well as membrane protein localization during cell-cell interactions.

Furthermore, it also widens the potential applicability for analyzing datasets from 3D organoid imaging and perhaps even intravital two-photon microscopy.

(2) The software in its current form only allows the broad demarcation of the cells examined into two populations: targets and effectors. This limits the number of cell populations that can be examined for their interactions. It might be more useful to just allow multiple user-defined populations instead of restricting the populations to target and effector cells only.

(3) Similarly, subsetting of each of the populations could be made more intuitive. Although it is possible to define subsets of cells using the "Custom classification" function under the "Measure" module with user-defined parameters, visualization of multiple groups remains unintuitive and it appears that only one custom classified group can be selected and visualized at any given time in the Signal Annotator under Measurement instead of allowing visualization of multiple (custom defined) groups of cells in different colors. It is also unclear how, if possible at all, to visualize a custom group of cells in the Signal Annotator under the Detect Events module.

Software issues:

(4) When initially tested on v1.3.9, the Segment module could not be initiated (with the error message AttributeError: 'WindowsPath' object has no attribute 'endswith' when attempting to run segmentation).<br /> Update: this has been fixed in v1.3.9.post4 dated February 7th, 2025.

(5) Further testing was then performed by downgrading the software to v1.3.1. While testing the ADCC demo experiment (https://celldetective.readthedocs.io/en/latest/adcc-example.html), the workflow was stuck at attempts to initiate the Detect Events step:

AssertionError: No signal matches with the requirements of the model ['dead_nuclei_channel_mean', 'area']. Please pass the signals manually with the argument selected_signals or add measurements. Abort.

(Update: fixed in the latest v1.3.9.post4 version dated February 7th, 2025)

(6) Random bugs causing the software to crash. Example: switching characteristic to 'status_color' in the Signal Annotator under Measurement caused the software to crash (v1.3.9.post4):

TypeError: ufunc 'isnan' is not supported for the input types, and the inputs could not be safely coerced to any supported types according to the casting rule 'safe'

(7) Overall, when exploring the functionality of the software, there have been multiple instances of software crashes when clicking/switching around to show different parameters, etc.

This reviewer understands the difficulties and time involved in bug fixing and hopes that the experience could have been much smoother and that the software behaves much more stably in order to maximize its useability.

Reviewer #2 (Public review):

Summary:

Immune assays enable the analysis of immune responses in vitro. These assays generate time series image data across several experimental conditions. The imaging parameters such as the imaging modality and the number of channels can vary across experiments. A challenge in the field is the lack of (open source) tools to process and analyze these data. R. Torro, et. al. developed an open source end-to-end pipeline for the analysis of image data from these immune assays. The pipeline is designed with a GUI and is suited for experimental biologists with no coding experience. The authors have incorporated several existing methods and tools for individual tasks such as for segmentation and cell tracking, and incorporated them with custom methods where necessary such as for tracking cell state transitions.

Strengths:

(1) The tool is extremely well-documented and easy to install.

(2) Applicable to a wide variety of imaging modalities and analysis.

(3) There are several different options for each step, such as segmentation using traditional methods or deep learning methods, and all the analysis steps are integrated in one place with a GUI. The no-coding requirement makes this a very powerful tool for biologists and has the potential to enable a wide variety of analyses.

Weakness:

(1) It would be good to provide documentation on how to make the tool applicable for applications and analysis other than for immune profiling since most methods integrated here are applicable well beyond immune profiling. For example, a user might want to use the tool just for the segmentation of their IF microscopy-images.

(2) They applied Celldetective to two immune assays. The authors present the results from these assays and use the results to validate their assay. However, they have not included data that demonstrates results obtained via this pipeline are comparable to results obtained with other pipelines and/or if these results are consistent with what is expected in the literature.

Author response:

In view of the suggestions of the referees, we wish to underline that a user can interact with celldetective at two levels: a non-coder can analyse data and train models without coding, but is necessarily offered pre-determined choices and flexibility. An advanced user however has practically limitless flexibility to extend the fully-open source celldetective, aided by its modularity and detailed manual.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Torro et al. presented CellDetective, an open-source software designed for a user-friendly execution of single-cell segmentation, tracking, and analysis of time-lapse microscopy data. The authors demonstrated the applications of the software by measuring NK cell spreading events acquired with reflection interference contrast microscopy (RICM), as well as detecting target cell death events and their interaction with neighboring NK cells in a multichannel widefield microscopy dataset.

Strengths:

The segmentation (StarDist, Cellpose) and tracking (bTrack) modules implemented were based on existing and published software packages. The authors added the event detection, classification, and analysis modules to enable an end-to-end time-lapse microscopy data processing and analysis pipeline, complete with a graphical user interface (GUI). This minimizes the coding experience required from the user. The documentation that accompanies CellDetective is also adequate.

Weaknesses:

Given that the software was designed to improve user experience, such an approach also limits its scope and functionality and is currently capable of handling very specific types of experiments. Additionally, this reviewer has also encountered many technical difficulties (see documented bugs/crashes below) that have prevented an extensive exploration of all the functionality of CellDetective.

We apologize for the technical difficulties and bugs; the ones mentioned have been already corrected. New users have also tested the installation and reported it to be bug-free.

We fully agree on the compromise that has to be found between user experience and versatility. We have already tested celldetective in other biological contexts, such as microbiology, but made a choice to showcase it in the article for immunological applications. We invite the reader to consult the software documentation and online examples to learn about more options.

Specifics:

(1) The software can only handle 2D 'widefield' time-lapse imaging datasets. It should be noted that many studies that examine cell-cell interactions in vitro also used confocal microscopy and acquired the time-lapse images in 3D z-stacks to enable the reconstruction of entire cell volumes from multiple optical sections along the z-axis.

Given that almost all of the implemented segmentation (StarDist, Cellpose) and tracking (bTrack) packages already support the handling of 3D datasets, it is unclear why CellDetective was designed to only work with 2D datasets.

As noted above, extending the support for 3D images would allow the scope and utility of this software to be further extended for imaging studies acquired in z-stacks. As an example, the dense clustering of effector cells in Figure 4 had prevented accurate segmentation due to the 2D nature of the experimental dataset. More importantly, support for a 3D dataset could also allow for the tracking of fluorescent protein-based sub-cellular as well as membrane protein localization during cell-cell interactions.

Furthermore, it also widens the potential applicability for analyzing datasets from 3D organoid imaging and perhaps even intravital two-photon microscopy.

We thank the reviewer for this suggestion. Indeed, extension to 3-dimensions is a natural development, since we have chosen segmentation and tracking methods which are compatible with 3D. However, two important strengths of celldetective are: harnessing statistical power of cell populations together with multiplexing biological conditions, and dynamic analysis of fast events.

For both, 2D is advantageous. Our own focus is on analyzing cellular events with minute time resolution, relevant in immunology. By our estimate (experience and literature), 3D timelapse acquisition would reduce the time resolution, as well as throughput (in terms of events and conditions) to below acceptable level. While we don’t envisage this upgrade in the immediate future, we encourage advanced users to contribute to further develop the open-source code in this direction. As a mitigation solution, a 2.5D approach on a flat sample by combining two z planes (in order to address issues of cell superposition for example), could be readily implemented with minimal change.

(2) The software in its current form only allows the broad demarcation of the cells examined into two populations: targets and effectors. This limits the number of cell populations that can be examined for their interactions. It might be more useful to just allow multiple user-defined populations instead of restricting the populations to target and effector cells only.

We thank the reviewer for this suggestion. There is little architectural limitation to its implementation; this will be proposed in the future version. This updated version will allow more than two user-defined populations, labelled directly by the user, which will also facilitate the natural extension to more varied biological applications. Three-way interactions are much more complex, and, to our knowledge, not currently addressed by biologists. The interactions will for the moment be limited to 2 populations interactions, as multipartite ones involve a higher level of code modifications, not immediately envisaged.

(3) Similarly, subsetting of each of the populations could be made more intuitive. Although it is possible to define subsets of cells using the "Custom classification" function under the "Measure" module with user-defined parameters, visualization of multiple groups remains unintuitive and it appears that only one custom classified group can be selected and visualized at any given time in the Signal Annotator under Measurement instead of allowing visualization of multiple (custom defined) groups of cells in different colors. It is also unclear how, if possible at all, to visualize a custom group of cells in the Signal Annotator under the Detect Events module.

The simultaneous visualization of several classes poses problems in the choice of colors and symbols, and may render the tool difficult to use. The time propagation option in the classification tool allows to define event classes as opposed to groups, that are compatible with the Signal Annotator. For more complex classifications, a simple solution is to work with composite classifications, which are already supported by using logical AND/OR operators on the condition defining the class. We believe that this feature is sufficient to address this issue.

Software issues:

(4) When initially tested on v1.3.9, the Segment module could not be initiated (with the error message AttributeError: 'WindowsPath' object has no attribute 'endswith' when attempting to run segmentation).

Update: this has been fixed in v1.3.9.post4 dated February 7th, 2025.

(5) Further testing was then performed by downgrading the software to v1.3.1. While testing the ADCC demo experiment (https://celldetective.readthedocs.io/en/latest/adcc-example.html), the workflow was stuck at attempts to initiate the Detect Events step:

AssertionError: No signal matches with the requirements of the model ['dead_nuclei_channel_mean', 'area']. Please pass the signals manually with the argument selected_signals or add measurements. Abort.

(Update: fixed in the latest v1.3.9.post4 version dated February 7th, 2025)

(6) Random bugs causing the software to crash. Example: switching characteristic to 'status_color' in the Signal Annotator under Measurement caused the software to crash (v1.3.9.post4):

TypeError: ufunc 'isnan' is not supported for the input types, and the inputs could not be safely coerced to any supported types according to the casting rule 'safe'

(7) Overall, when exploring the functionality of the software, there have been multiple instances of software crashes when clicking/switching around to show different parameters, etc.

This reviewer understands the difficulties and time involved in bug fixing and hopes that the experience could have been much smoother and that the software behaves much more stably in order to maximize its useability.

We apologize again for the various technical issues encountered during the review process, and thank the reviewer for mentioning that several bugs were already fixed in the last software release. The open source and software maintenance protocol enabled by github should help to resolve any further emerging issue.

Reviewer #2 (Public review):

Summary:

Immune assays enable the analysis of immune responses in vitro. These assays generate time series image data across several experimental conditions. The imaging parameters such as the imaging modality and the number of channels can vary across experiments. A challenge in the field is the lack of (open source) tools to process and analyze these data. R. Torro, et. al. developed an open source end-to-end pipeline for the analysis of image data from these immune assays. The pipeline is designed with a GUI and is suited for experimental biologists with no coding experience. The authors have incorporated several existing methods and tools for individual tasks such as for segmentation and cell tracking, and incorporated them with custom methods where necessary such as for tracking cell state transitions.

Strengths:

(1) The tool is extremely well-documented and easy to install.

(2) Applicable to a wide variety of imaging modalities and analysis.

(3) There are several different options for each step, such as segmentation using traditional methods or deep learning methods, and all the analysis steps are integrated in one place with a GUI. The no-coding requirement makes this a very powerful tool for biologists and has the potential to enable a wide variety of analyses.

Weakness:

(1) It would be good to provide documentation on how to make the tool applicable for applications and analysis other than for immune profiling since most methods integrated here are applicable well beyond immune profiling. For example, a user might want to use the tool just for the segmentation of their IF microscopy-images.

This is an important suggestion that we will implement as short demonstrations using data from the public domain. These will be proposed as examples in the online documentation.

(2) They applied Celldetective to two immune assays. The authors present the results from these assays and use the results to validate their assay. However, they have not included data that demonstrates results obtained via this pipeline are comparable to results obtained with other pipelines and/or if these results are consistent with what is expected in the literature.

In the final version of the article, we shall compare celldetective with existing literature, including our previous work, when possible. However, we emphasize that most of the presented data are original and don’t have any published equivalent in the literature. Concerning the immunotherapy assays, data presented already show expected trends (see for example Fig. 2 and Fig. 5). We reserve for future publications the systematic comparison with traditional (non microscopy-based) methods, as we consider it out-of-scope here. Additionally, there is, to our knowledge no existing open pipeline performing the full end-to-end analysis.

eLife Assessment

This manuscript describes the characterization of the conformational dynamics of two chemokine receptors at the single-molecule level using FRET. The authors make a convincing case for attributing the distinct interaction and pharmacology of the two receptors to differences in their conformational energy landscape. These important findings will be of interest to scientists working on activation mechanisms of GPCRs and signal transduction.

Joint Public Review:

Summary

This manuscript uses single-molecule fluorescence resonance energy transfer (smFRET) to identify differences in the molecular mechanisms of CXCR4 and ACKR3, two 7-transmembrane receptors that both respond to the chemokine CXCL12 but otherwise have very different signaling profiles. CXCR4 is highly selective for CXCL12 and activates heterotrimeric G proteins. In contrast, ACKR3 is quite promiscuous and does not couple to G proteins, but like most G protein-coupled receptors (GPCRs), it is phosphorylated by GPCR kinases and recruits arrestins. By monitoring FRET between two positions on the intracellular face of the receptor (which highlight the movement of transmembrane helix 6 [TM6], a key hallmark of GPCR activation), the authors show that CXCR4 remains mostly in an inactive-like state until CXCL12 binds and stabilizes a single active-like state. ACKR3 rapidly exchanges among four different conformations even in the absence of ligand, and agonists stabilize multiple activated states.

Strengths

The core method employed in this paper, smFRET, can reveal dynamic aspects of these receptors (the breadth of conformations explored and the rate of exchange among them) that are not evident from static structures or many other biophysical methods. smFRET has not been broadly employed in studies of GPCRs. Therefore, this manuscript makes important conceptual advances in our understanding of how related GPCRs can vary in their conformational dynamics.

Weaknesses

The probes used cannot reveal conformational changes in other positions besides transmembrane helix 6 (TM6). GPCRs are known to exhibit loose allosteric coupling, so the conformational distribution observed at TM6 may not fully reflect the global conformational distribution of receptors. This could mask important differences that determine the ability of intracellular transducers to couple to specific receptor conformations.

While it is clear that CXCR4 and ACKR3 have very different conformational dynamics, the data do not definitely show that this is the main or only mechanism that contributes to their functional differences.

The extent to which conformational heterogeneity is a characteristic feature of ACKRs that contributes to their promiscuity and arrestin bias is unclear. The key residue the authors find promotes ACKR3 conformational heterogeneity is not conserved in most other ACKRs, but alternative mechanisms could generate similar heterogeneity.

An inherent limitation of the approach is that mutagenesis, purification, and labeling of the receptors could affect their conformational distributions. The cysteine mutations in ACKR3 required to site-specifically install fluorophores substantially increase its ligand-induced activity (Fig. S1D). There are no data to confirm that the two receptors retain the same functional profiles observed in cell-based systems following in vitro manipulations (purification, labeling, nanodisc reconstitution).

Author response:

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

Reviewer #1 (Public Review):

Summary:

This paper uses single-molecule FRET to investigate the molecular basis for the distinct activation mechanisms between 2 GPCR responding to the chemokine CXCL12 : CXCR4, that couples to G-proteins, and ACKR3, which is G-protein independent and displays a higher basal activity.

Strengths:

It nicely combines the state-of-the-art techniques used in the studies of the structural dynamics of GPCR. The receptors are produced from eukaryotic cells, mutated, and labeled with single molecule compatible fluorescent dyes. They are reconstituted in nanodiscs, which maintain an environment as close as possible to the cell membrane, and immobilized through the nanodisc MSP protein, to avoid perturbing the receptor's structural dynamics by the use of an antibody for example.

The smFRET data are analysed using the HHMI technique, and the number of states to be taken into account is evaluated using a Bayesian Information Criterion, which constitutes the state-of-the-art for this task.

The data show convincingly that the activation of the CXCR4 and ACKR3 by an agonist leads to a shift from an ensemble of high FRET states to an ensemble of lower FRET states, consistent with an increase in distance between the TM4 and TM6. The two receptors also appear to explore a different conformational space. A wider distribution of states is observed for ACKR3 as compared to CXCR4, and it shifts in the presence of agonists toward the active states, which correlates well with ACKR3's tendency to be constitutively active. This interpretation is confirmed by the use of the mutation of Y254 to leucine (the corresponding residue in CXCR4), which leads to a conformational distribution that resembles the one observed with CXCR4. It is correlated with a decrease in constitutive activity of ACKR3.

Weaknesses:

Although the data overall support the claims of the authors, there are however some details in the data analysis and interpretation that should be modified, clarified, or discussed in my opinion

Concerning the amplitude of the changes in FRET efficiency: the authors do not provide any structural information on the amplitude of the FRET changes that are expected. To me, it looks like a FRET change from ~0.9 to ~0.1 is very important, for a distance change that is expected to be only a few angstroms concerning the movement of the TM6. Can the authors give an explanation for that? How does this FRET change relate to those observed with other GPCRs modified at the same or equivalent positions on TM4 and TM6?

The large FRET change in our system was initially unexpected. However, the reviewer is mistaken that the expected distance change is only a few angstroms. Crystal structures of the homologous beta2 adrenergic receptor (β₂AR) in inactive and active conformations reveal that the cytoplasmic end of TM6 moves outwards by 16 angstroms during activation (Rasmussen et al., 2011, ref 47).  Consistent with this, smFRET studies of β₂AR labeled in TM4 and TM6 (as here) showed that the donor-acceptor (D-A) distance was 14 angstroms longer in the active conformation (Gregorio et al., ref 38).  Surprisingly, the apparent distance change in our system (calculated for our FRET probes, A555/Cy5, using FPbase.com) is almost 30 angstroms. A possible explanation is that the fluorophore attached to TM6 interacts with lipids within the nanodisc when TM6 moves outwards, which could stretch the fluorophore linker and thereby increase the D-A distance (lipids were absent in the β₂AR study). Such an interaction could also constrain the fluorophore in an unfavorable orientation for energy transfer, also leading to lower than expected FRET efficiencies and inflated distance calculations. Regardless, it is important to emphasize that none of the interpretations or conclusions of our study are based on computed D-A distances. Rather, we resolved different receptor conformations and quantified their relative populations based on the measured FRET efficiency distributions.

Finally, we note that a recent smFRET study of the glucagon receptor (labeled in TM4 and TM6, as here) also revealed a large difference in apparent FRET efficiencies between inactive (E_app = 0.83) and active (E_app = 0.32) conformations (Kumar et al., ref. 39). Thus, the large change in FRET efficiency observed in our study is not unprecedented.

Concerning the intermediate states: the authors observe several intermediate states.

(1) First I am surprised, looking at the time traces, by the dwell times of the transitions between the states, which often last several seconds. Is such a long transition time compatible with what is known about the kinetic activation of these receptors?

We too were surprised by the apparent kinetics of the receptors in our system. However, it was previously noted that purified systems, including nanodiscs, lead to slower activation times for GPCRs compared to cellular membrane systems (Lohse et al, Curr. Opin. Cell Biology, 27, 8792, 2014). Indeed, slow transitions among different FRET states (dwell times in the seconds range) were also observed in recent smFRET studies of the mu opioid receptor (Zhao et al., 2024, ref. 41) and the glucagon receptor (Kumar et al., 2023, ref. 39). These studies are consistent with the observed time scale of the FRET transitions reported here.

(2) Second is it possible that these “intermediate” states correspond to differences in FRET efficiencies, that arise from different photophysical states of the dyes? Alexa555 and Cy5 are Cyanines, that are known to be very sensitive to their local environment. This could lead to different quantum yields and therefore different FRET efficiencies for a similar distance. In addition, the authors use statistical labeling of two cysteines, and have therefore in their experiment a mixture of receptors where the donor and acceptor are switched, and can therefore experience different environments. The authors do not speculate structurally on what these intermediate states could be, which is appreciated, but I think they should nevertheless discuss the potential issue of fluorophore photophysics effects.

The reviewer is correct that the intermediate FRET states could, in principle, arise from a conformational change of the receptor that alters the local environment of the donor and/or acceptor fluorophores, rather than a change in donor-acceptor distance. This caveat is now included in the discussion on Pg. 10:

“In principle, the intermediates in CXCR4 and ACKR3 could represent partial movements of TM6 from the inactive to active conformation or more subtle conformational changes altering the photophysical characteristics of the probes without drastically altering the donor-acceptor distance. Either possibility leads to detectable changes in apparent FRET efficiency and reflect discrete conformational steps on the activation pathway; however, it is not possible to resolve specific structural changes from the data.”

Regarding the second possibility, it is true that our labeling methodology leads to a statistical mixture of labeled species (D on TM6 and A on TM4, D on TM4 and A on TM6). If the photophysical properties of the fluorophores were markedly different for the two labeling orientations, this would produce two different FRET efficiencies for a given receptor conformation. Assuming two receptor conformations, this scenario would produce four distinct FRET states: E₁ (inactive receptor, labeling configuration 1), E₂ (active receptor, labeling configuration 1), E₃ (inactive receptor, labeling configuration 2) and E₄ (active receptor, labeling configuration 2), with two cross peaks in the TDP plots, corresponding to E₁ ↔ E₂ and E₃ ↔ E₄ transitions. Notably, E₂ ↔ E₃ cross peaks would not be present, since states E₂ and E₃ exist on separate molecules. Instead, we see all states inter-connected sequentially, R ↔ R’ ↔ R* in CXCR4 and R ↔ R’ ↔ R*’ ↔ R* in ACKR3 (Fig. 2), suggesting that the resolved FRET states represent interconnected conformational states.

We added the following text to the Results section on Pg. 6:

“Two-dimensional transition density probability (TDP) plots revealed that the three FRET states were connected in a sequential fashion (Figs. 2A & B), indicating that the transitions occurred within the same molecules. Notably, these observations exclude the possibility that the midFRET state arises from different local fluorophore environments (hence FRET efficiencies) for the two possible labeling orientations of the introduced cysteines: assuming two receptor conformations, this model would produce four distinct FRET states, but only two cross peaks in the TDP plot.”

(3) It would also have been nice to discuss whether these types of intermediate states have been observed in other studies by smFRET on GPCR labeled at similar positions.

Intermediate states have also been reported in previous smFRET studies of other GPCRs. For example, in the glucagon receptor (also labeled in TM4 and TM6), a third FRET state (E_app =  0.63) was resolved between the inactive (E_app  = 0.85) and active (E_app  = 0.32) states (Kumar et al., Ref. 39).  Discrete intermediate receptor conformations were also observed in the A_2AR labeled in TM4 and TM6 (Fernandes et al., Ref 40). These examples are now cited in the Discussion.

On line 239: the authors talk about the R↔R' transitions that are more probable. In fact it is more striking that the R'↔R* transition appears in the plot. This transition is a signature of the behavior observed in the presence of an agonist, although IT1t is supposed to be an inverse agonist. This observation is consistent with the unexpected (for an inverse agonist) shift in the FRET histogram distribution. In fact, it appears that all CXCR4 antagonists or inverse agonists have a similar (although smaller) effect than the agonist. Is this related to the fact that these (antagonist or inverse agonist) ligands lead to a conformation that is similar to the agonists, but cannot interact with the G-protein ?? Maybe a very interesting experiment would be here to repeat these measurements in the presence of purified G-protein. G-protein has been shown to lead to a shift of the conformational space explored by GPCR toward the active state (using smFRET on class A and class C GPCR). It would be interesting to explore its role on CXCR4 in the presence of these various ligands. Although I am aware that this experiment might go beyond the scope of this study, I think this point should be discussed nevertheless.

We thank the reviewer for this observation and the possible explanation offered.  In response, we have added the following text to the Results section on Pg. 7:

“The small-molecule ligand IT1t is reported to act as an inverse agonist of CXCR4 (54-56). However, the conformational distribution of CXCR4 showed little change to the overall apparent

FRET profile, although R’ ↔ R* transitions appeared in the TDP plot (Figs. 3A & B, Fig. S8). This suggests that the small molecule does not suppress CXCR4 basal signaling by changing the conformational equilibrium. Instead IT1t appears to increase transition probabilities which may impair G protein coupling by CXCR4.”

We have also added the following text to the Results on Pg. 8:

“Despite the ability of CXCL12_P2G and CXCL12_LRHQ to stabilize the active R* conformation of CXCR4, both variants are known to act as antagonists (20). This suggests that the CXCL12 mutants inhibit CXCR4 coupling to G proteins not by suppressing the active receptor population but rather by increasing the dynamics of the receptor state transitions. Our results suggest that the helical movements considered classic signatures of the active state may not be sufficient for CXCR4 to engage productively with G proteins.”

In addition, we have added the following text to the Discussion on Pg. 11:

“The chemokine variants CXCL12_P2G and CXCL12_LRHQ are reported to act as antagonists of CXCR4 (19, 20), and the small molecule IT1t acts as an inverse agonist (54-56). Surprisingly, none of these ligands inhibit formation of the active R* conformation of CXCR4. In fact, the chemokine variants both stabilize and increase this state to some degree, although less effectively than CXCL12_WT. Thus, the antagonism and inverse agonism of these ligands does not appear to be linked exclusively to receptor conformation, suggesting that the ligands inhibit coupling of G proteins to CXCR4 or disrupt the ligand-receptor-G protein interaction network required for signaling (Fig. S10) (21, 23).  Interestingly, these ligands also increase the probabilities of state-to-state transitions (Figs. 3B & 4B), suggesting that enhanced conformational exchange prevents the receptor from productively engaging G proteins. Similarly, ACKR3 is naturally dynamic and lacks G protein coupling, suggesting a common mechanism of G protein antagonism.”

Finally, we also agree that experiments with G proteins could be informative. In fact, we initiated such experiments during the course of this study.  However, it soon became apparent that significant optimization would be required to identify fluorophore labeling positions that report receptor conformation without inhibiting G protein coupling. Accordingly, we decided that G protein experiments would be the subject of future studies.

However, we added the following text to the Discussion on Pg. 12:

“Future smFRET studies performed in the presence of G proteins should be informative in this regard”.

The authors also mentioned in Figure 6 that the energetic landscape of the receptors is relatively flat ... I do not really agree with this statement. For me, a flat conformational landscape would be one where the receptors are able to switch very rapidly between the states (typically in the submillisecond timescale, which is the timescale of protein domain dynamics). Here, the authors observed that the transition between states is in the second timescale, which for me implies that the transition barrier between the states is relatively high to preclude the fast transitions.

We thank the reviewer for the comment. We have modified the description of the energy landscapes of ACKR3 and CXCR4 in the discussion on Pg. 10 as follows:

“These observations imply that ACKR3 has a relatively flat energy landscape, with similar energy minima for the different conformations, whereas the energy landscape of CXCR4 is more rugged (Fig. 6). For both receptors, the energy barriers between states are sufficiently high that transitions occur relatively slowly with seconds long dwell times (Figs. 1C and S2).”

Reviewer #2 (Public Review):

Summary:

his manuscript uses single-molecule fluorescence resonance energy transfer (smFRET) to identify differences in the molecular mechanisms of CXCR4 and ACKR3, two 7transmembrane receptors that both respond to the chemokine CXCL12 but otherwise have very different signaling profiles. CXCR4 is highly selective for CXCL12 and activates heterotrimeric G proteins. In contrast, ACKR3 is quite promiscuous and does not couple to G proteins, but like most G protein-coupled receptors (GPCRs), it is phosphorylated by GPCR kinases and recruits arrestins. By monitoring FRET between two positions on the intracellular face of the receptor (which highlights the movement of transmembrane helix 6 [TM6], a key hallmark of GPCR activation), the authors show that CXCR4 remains mostly in an inactive-like state until CXCL12 binds and stabilizes a single active-like state. ACKR3 rapidly exchanges among four different conformations even in the absence of ligands, and agonists stabilize multiple activated states.

Strengths:

The core method employed in this paper, smFRET, can reveal dynamic aspects of these receptors (the breadth of conformations explored and the rate of exchange among them) that are not evident from static structures or many other biophysical methods. smFRET has not been broadly employed in studies of GPCRs. Therefore, this manuscript makes important conceptual advances in our understanding of how related GPCRs can vary in their conformational dynamics.

Weaknesses:

(1) The cysteine mutations in ACKR3 required to site-specifically install fluorophores substantially increase its basal and ligand-induced activity. If, as the authors posit, basal activity correlates with conformational heterogeneity, the smFRET data could greatly overestimate the conformational heterogeneity of ACKR3.

The change in basal ACKR3 activity with the Cys introductions are modest in comparison and insignificantly different as determined by extra-sum-of-squares F test (P=0.14).

(2) The probes used cannot reveal conformational changes in other positions besides TM6. GPCRs are known to exhibit loose allosteric coupling, so the conformational distribution observed at TM6 may not fully reflect the global conformational distribution of receptors. This could mask important differences that determine the ability of intracellular transducers to couple to specific receptor conformations.

We agree that the overall conformational landscape of the receptors has not been investigated and we have added this caveat to the discussion on Pg. 12.

“An important caveat is that our study does not report on the dynamics of the other TM helices and H8, some of which are known to participate in arrestin interactions.”

(3) While it is clear that CXCR4 and ACKR3 have very different conformational dynamics, the data do not definitively show that this is the main or only mechanism that contributes to their functional differences. There is little discussion of alternative potential mechanisms.

The main functional difference between CXCR4 and ACRK3 is their effector coupling: CXCR4 couples to G proteins, whereas ACKR3 only couples to arrestins (following phosphorylation of the C-terminal tail by GRKs). As currently noted in the discussion, ACKR3 has many features that may contribute to its lack of G protein coupling, including lack of a well-ordered intracellular pocket due to conformational dynamics, lack of an N-term-ECL3 disulfide, different chemokine binding mode, and the presence of Y257. Steric interference due to different ICL loop structures may also interfere with G protein activation. No one thing has proven to confer ACKR3 with G protein activity including swapping all of the ICLs to those of canonical chemokine receptor, suggesting it is a combination of these different factors. The following has been added to the discussion on Pg. 13 to clearly note that any one feature is unlikely to drive the atypical behavior of ACKR3:

“The atypical activation of ACKR3 does not appear to be dependent on any singular receptor feature and is likely a combination of several factors.”

(4) The extent to which conformational heterogeneity is a characteristic feature of ACKRs that contributes to their promiscuity and arrestin bias is unclear. The key residue the authors find promotes ACKR3 conformational heterogeneity is not conserved in most other ACKRs, but alternative mechanisms could generate similar heterogeneity.

Despite the commonalities in the roles of the ACKRs, they all appear to have evolved independently. Thus, we do not believe that all features observed and described for one ACKR will explain the behavior of another. We have carefully avoided expanding our observations to other ACKRs to avoid suggesting common mechanisms.

(5) There are no data to confirm that the two receptors retain the same functional profiles observed in cell-based systems following in vitro manipulations (purification, labeling, nanodisc reconstitution).

We agree this is an important point. All labeled receptors responded to agonist stimulation as expected. As only properly folded receptors are able to make the extensive interactions with ligands necessary for conformational changes (for instance, CXCL12 interacts with all TMs and ECLs), this suggests that the proteins are folded correctly and functional following all manipulations.

Reviewer #3 (Public Review):

Summary:

This is a well-designed and rigorous comparative study of the conformational dynamics of two chemokine receptors, the canonical CXCR4 and the atypical ACKR3, using single-molecule fluorescence spectroscopy. These receptors play a role in cell migration and may be relevant for developing drugs targeting tumor growth in cancers. The authors use single-molecule FRET to obtain distributions of a specific intermolecular distance that changes upon activation of the receptor and track differences between the two receptors in the apo state, and in response to ligands and mutations. The picture emerging is that more dynamic conformations promote more basal activity and more promiscuous coupling of the receptor to effectors.

Strengths:

The study is well designed to test the main hypothesis, the sample preparation and the experiments conducted are sound and the data analysis is rigorous. The technique, smFRET, allows for the detection of several substates, even those that are rarely sampled, and it can provide a "connectivity map" by looking at the transition probabilities between states. The receptors are reconstituted in nanodiscs to create a native-like environment. The examples of raw donor/acceptor intensity traces and FRET traces look convincing and the data analysis is reliable to extract the sub-states of the ensemble. The role of specific residues in creating a more flat conformational landscape in ACKR3 (e.g., Y257 and the C34-C287 bridge) is well documented in the paper.

Weaknesses:

The kinetics side of the analysis is mentioned, but not described and discussed. I am not sure why since the data contains that information. For instance, it is not clear if greater conformational flexibility is accompanied by faster transitions between states or not.

The reviewer is correct that kinetic information is available, in principle, from smFRET experiments. However, a detailed kinetic analysis will require a much larger data set than we currently possess, to adequately sample all possible transitions and the dwell times of each FRET state. We intend to perform such an analysis in the future as more data becomes available. The purpose of this initial study was to explore the conformational landscapes of CXCR4 and ACKR3 and to reveal differences between them. To this end, we have documented major differences in conformational preferences and response to ligands of the two receptors that are likely relevant to their different biological behavior. Future kinetic information will add further detail, but is not expected to alter the conclusions drawn here.

The method to choose the number of states seems reasonable, but the "similarity" of states argument (Figures S4 and S6) is not that clear.

We thank the reviewer for noting a need for further clarification. We qualitatively compared the positions of the various FRET peaks across treatments to gain insight into the consistency of the conformations and avoid splitting real states by overfitting the data. For instance, fitting the ACKR3 treatments with three states leads to three distinct FRET populations for the R’ intermediate. Adding a fourth state results in two intermediates that are fairly well overlapping. In contrast, the two-intermediate model for CXCR4 appears to split the R* state of the CXCL12 treated sample and causes a general shift in both intermediate states to lower FRET values when CXCL12 is present. As we assume that the conformations are consistent throughout the treatments, we conclude that this represents an overfitting artifact and not a novel CXCL12CXCR4 R*’ state. Additional sentences have been added to the supplemental figure legend to better describe the comparative analysis.

“(Top) With the 3-state model, the R’ states for apo-CXCR4 and for CXCL12- and IT1t-bound receptor overlapped well with similar apparent FRET values across all of the tested conditions. In the case of the four-state model, the R*’ (Middle) and R’ (Bottom) states were substantially different across the ligand treatments. In particular, the R*’ state with CXCL12 treatment appears to arise from a splitting of the R* conformation, indicating that the model was overfitting the data.”

Also, the "dynamics" explanation offered for ACKR3's failure to couple and activate G proteins is not very convincing. In other studies, it was shown that activation of GPCRs by agonists leads to an increase in local dynamics around the TM6 labelling site, but that did not prevent G protein coupling and activation.

We agree with the reviewer that any single explanation for ACKR3 bias, including the dynamics argument presented here, is insufficient to fully characterize the ACKR3 responses. As noted by the reviewer, the TM6 movement and dynamics is generally correlated with G protein coupling, whereas other dynamics studies (Wingler et al. Cell 2019) have noted that arrestinbiased ligands do not lead to the same degree of TM6 movement. We have added the following statement to the discussion on Pg. 13:

“The atypical activation of ACKR3 does not appear to be dependent on any singular receptor feature and is likely a combination of several factors.” 

Recommendations for the authors:  

Reviewer #1 (Recommendations For The Authors):

I would like to raise a technical point about the calculation and reporting of the FRET efficiency. The authors report the FRET efficiency as E=IA/(IA+ID). There is now a strong recommendation from the FRET community (https://doi.org/10.1038/s41592-018-0085-0) to use the term “FRET efficiency” only when a proper correction procedure of all correction factors has been applied, which is not the case here (gamma factor has not been calculated). The authors should therefore use the term “Apparent FRET Efficiency” and  E_app in all the manuscripts.

Also, it would be nice to indicate directly on the figures whether a ligand that is used is an agonist, antagonist, inverse agonist, etc...

We thank the reviewer for suggesting this clarification in terminology. We now refer to apparent FRET efficiency (or E_app) throughout the manuscript and in the figures. In addition, we have added ligand descriptions to the relevant figures.

Reviewer #2 (Recommendations For The Authors):

(1) M159(4.40)C/Q245(6.28)C ACKR3 appears to have higher constitutive activity than ACKR3 Wt (Fig. S1). While the vehicle point itself is likely not significant due to the error in the Wt, the overall trend is clear and arguably even stronger than the effect of Y257(6.40)L (Fig. S9). While this is an inherent limitation of the method used, it should be clearly acknowledged; the comment in lines 162-164 seems to skirt the issue by only saying that arrestin recruitment is retained. It would be helpful and more rigorous to report the curve fit parameters (basal, E_max, EC50) for the arrestin recruitment experiments and the associated errors/significance (see https://www.graphpad.com/guides/prism/latest/statistics/stat_qa_multiple_comparisons_ after_.htm for a discussion).

The Emin, E_max, and EC50 for M159⁴.⁴⁰C/Q245⁶.²⁸C ACKR3 were compared against the values for WT ACKR3 from Fig. S1 and only the E_max was determined to be significantly different by the extra sum of squares F test. A note has been added to the text to reflect these results on Pg. 5.

“Only the E_max for arrestin recruitment to CXCL12-stimulated ACKR3 was significantly altered by the mutations, while all other pharmacological parameters were the same as for WT receptors.”

(2) The methods do not specify the reactive group of the dyes used for labeling (i.e., AlexaFluor 555-maleimide and Cy5-maleimide?).

We regret the omission and have added the necessary details to the materials and methods.

(3) Were any of the native Cys residues removed from ACKR3 and CXCR4 in the constructs used for smFRET? ACKR3 appears to have two additional Cys residues in the N-terminus besides the one involved in the second disulfide bridge, and these would presumably be solvent-exposed. If so, please specify in the Methods and clarify whether the constructs tested in functional assays included these. (Also, please specify if the human receptors were used.)

No additional cysteine residues were mutated in either receptor. All exposed cysteines are predicted to form disulfides. The residues in the N-terminus that the reviewer alludes to, C21 and C26, form a disulfide (Gustavsson et al. Nature Communications 2017) and are thus protected from our probes. Consistent with these expectations, neither WT CXCR4 nor ACKR3 exhibited significant fluorophore labeling (now mentioned in the text on Pg. 5). The species of origin has been added to the material and methods.

(4) There are a few instances where the data seem to slightly diverge from the proposed models that may be helpful to comment on explicitly in the text:

- Figure 4E (ACKR3/CXCL12(P2G)): As noted in the legend, despite stabilizing R*/R*', CXCL12(P2G) reduces transitions between these states compared to Apo. This is more similar to the effects of VUF16840 (Figure 3D) than the other ACKR3 agonists. The authors note the difference between CXCL12(LHRQ) and CXCL12(P2G) (but not vs Apo) in this regard. There might be some other information here regarding the relative importance of the conformational equilibrium vs transition rates for receptor activity.

Although the TDPs for CXCL12_P2G and VUF16840 are similar, as noted by the reviewer, the overall FRET envelopes are drastically different.

The differences in transition probabilities for R ↔ R’ and R*’ « R* transitions observed in the presence of CXCL12_P2G or CXCL12_LRHQ relative to the apo receptor are now explicitly noted in the Results.

- The conformational distributions of ACKR3 apo and ACKR3 Y257L CXCL12 are very similar (Figure 5A,D). However, there is a substantial difference in the basal activity of WT vs CXCL12stimulated Y257L (Figure S9).

The mutation Y257L appears to promote the highest and lowest FRET states at the expense of the intermediates. Although the distribution appears similar between Apo-WT and CXCL12Y257L, the depopulation of the R’ state may lead to the observed activation in cells.

(5) There are inconsistent statements regarding the compatibility of G protein binding to the "active-like" ACKR3 conformation observed in the authors' previous structures (Yen et al, Sci Adv 2022). In the introduction, the authors seem to be making the case that steric clashes cannot account for its lack of coupling; in the discussion, they seem to consider it a possibility.

The introduction to previous research on the molecular mechanisms governing the lack of ACKR3-G protein coupling was not intended to be all encompassing, but rather to highlight previous efforts to elucidate this process and justify our study of the role  of dynamics. Due to the positions of the probes, we can only comment on the impact on TM6 movements and not other conformational changes. The steric clash reported in Yen et al. was in ICL2 and not directly tested here, so our observations do not preclude changes occurring in this region. We also do not claim that the active-like state resolved in our previous structures matches any specific state isolated here by smFRET.

(6) Line 83-85: "Having excluded other mechanisms we therefore surmised that the inability of ACKR3 to activate G proteins may be due to differences in receptor dynamics."

Line 400-402: "It is possible that the active receptor conformation clashes sterically with the G protein as suggested by docking of G proteins to structures of ACKR3."

As mentioned above, we suspect the mechanisms governing the inability of  ACKR3 to couple to G proteins may be more complex than one particular feature but instead due to a combination of several factors. Accordingly, we have not completely eliminated a contribution of steric hindrance as we described in Yen et al. Sci Adv 2022 and instead include it as a possibility. Following the line highlighted here, we list several alternatives: 

“Alternatively, the receptor dynamics and conformational transitions revealed here may prevent formation of productive contacts between ACKR3 and G protein that are required for coupling, even though G proteins appear to constitutively associate with the receptor.”

And, at the end of the paragraph, we have added the following sentence: 

“The atypical activation of ACKR3 does not appear to be dependent on any singular receptor feature and is likely a combination of several factors.”

(7) If the authors believe that the various ligands/mutations are only altering the distribution/dynamics of the same 3/4 conformations of CXCR4/ACKR3, respectively, is there a reason each FRET efficiency histogram is fit independently instead of constraining the individual components to Gaussian components with the same centroids, and/or globally fitting all datasets for the same receptor?

We performed global analysis across all data sets for each sample and condition. Since the peak positions of the various FRET states recovered in this way were consistent across treatments (Fig. S4,S6), we did not feel it was necessary to perform a further global analysis across all samples for a given receptor.

Reviewer #3 (Recommendations For The Authors):

The manuscript is well-written, the arguments are easy to follow and the figures are helpful and clear. Here are a few questions/suggestions that the authors might want to address before the paper will be published:

(1) Include a table with kinetic rates between states in SI and have a brief discussion in the main text to support the trends observed in transition probabilities.

As noted above, determining rate constants for each of the state-to-state transitions will require a much larger set of experimental smFRET data than is currently available and will be the subject of future studies.

(2) The argument of state similarity (Figure S4 and S6)... why are the profiles not Gaussian, like in the fits on Figures S3 and S5, repectively? I would also suggest that once the number of states is chosen to do a global fit, where the FRET values of a certain sub-state across different conditions for one receptor are shared.

The state distributions presented in Figs. S4 and S6 (as well as throughout the rest of the paper) are derived from HMM fitting of the time traces themselves, and are not constrained to be Gaussian, whereas the GMM analysis in Figs. S3 and S5 are Gaussian fits to the final apparent FRET efficiency histograms.

Similar to our response to Review 2 above, due to the consistency of the fitted peak positions obtained across different conditions for a given sample, we did not feel that further global analysis was necessary.

(3) It is shown FRET changes from ~0.85 in the inactive (closed) state to ~0.25 in the active (open) state. How do these values match the expectations based on crystal structure and dye properties?

As noted in our response to Reviewer 1, translating the apparent FRET values using the assumed Förster distances for A555/Cy5 (per FPbase) suggest a change in D-A distance of ~30 angstroms, whereas the expected change from structures is ~16 Å. We suspect this discrepancy is due to the lipids immediately adjacent to the fluorophores, which may lead to the probes being constrained in an extended position when TM6 moves outwards, thus also reporting the linker length in the distance change. Additionally, such interactions may constrain the donor and acceptor in unfavorable orientations for energy transfer, which would also reduce the FRET efficiency in the active state. Since the calculated D-A distance changes appear too large for GPCR activation, we have opted to not make any structural interpretations. Instead, all of our conclusions are based on resolving individual conformational states and quantifying their relative populations, which is based directly on the measured FRET efficiency distributions, not computed distances.

(4) The results on the effect of CXCL12-P2G on CXCR4 are confusing...despite being an antagonist, this ligand stabilizes the "active state"...I am not sure if the explanation offered is sufficient that the opening of the intracellular cleft is not sufficient to drive the G protein coupling/activation.

We agree that the explanation related to the opening of the intracellular cleft being insufficient to drive G protein coupling/activation is speculative and we have removed that text. We now simply propose that the CXCL12 variants inhibit coupling of G proteins to CXCR4 or disrupt interactions necessary for signaling, as stated in the following text to the results on Pg. 8:

“Despite the ability of CXCL12_P2G and CXCL12_LRHQ to stabilize the active R* conformation of CXCR4, both variants are known to act as antagonists (20). This suggests that the CXCL12 mutants inhibit CXCR4 coupling to G proteins not by suppressing the active receptor population but rather by increasing the dynamics of the receptor state-to-state transitions. Our results suggest that the helical movements considered classic signatures of the active state may not be sufficient for CXCR4 to engage productively with G proteins.”

eLife Assessment

This manuscript focuses on understanding if and how the glycosylation of SARS-CoV2 spike protein affects a putative allosteric network of interactions controlled by the binding of a fatty acid. The main conclusion is that glycans do not significantly affect the network of allosteric interactions. This valuable information - albeit mainly consisting of negative results - is based on convincing evidence. It will be of interest to scientists focusing on SARS CoV2 protein structure and dynamics.

Reviewer #1 (Public Review):

Summary:

The investigation delves into allosteric modulation within the glycosylated SARS-CoV-2 spike protein, focusing on the fatty acid binding site. This study uncovers intricate networks connecting the fatty acid site to crucial functional regions, potentially paving the way for developing innovative therapeutic strategies.

Strengths:

This article's key strength lies in its rigorous use of dynamic nonequilibrium molecular dynamics (D-NEMD) simulations. This approach provides a dynamic perspective on how the fatty acid binding site influences various functional regions of the spike. A comprehensive understanding of these interactions is crucial in deciphering the virus's behavior and identifying potential targets for therapeutic intervention.

Reviewer #2 (Public Review):

This is a nice paper illustrating the use of equilibrium/non-equilibrium MD simulations to explore allosteric communication in the Spike protein. The results are described in detail and suggest a complex network of signal transmission patterns. The topic is not completely novel as it has been studied before by the same authors and the impact of glycosylation is moderated and localized at the furin site, so not many new conclusions emerge here. It is suggested that mutations are commonly found in the communication pathway which is interesting, but the authors fail to provide evidence that this is related to a positive selection and not simply to a random effect related to mutations at points that are not crucial for stability or function. One interesting point is the connection of the FA site with an additional site binding heme group. It will be interesting to see reversibility, i.e. removal of the ligand at this site is producing perturbation at the FA site?, does it produce other effects suggesting a cascade of allosteric effects? Finally, the paper lacks details to help reproducibility, in particular, I do not see details on D-NEMD calculations. One interesting point is the connection of the FA site with an additional site binding heme group.

Reviewer #3 (Public Review):

Summary:

In a previous study, the authors analyzed the dynamics of the SARS-CoV2 spike protein through lengthy MD simulations and an out-of-equilibrium sampling scheme. They identified an allosteric interaction network linking a lipid-binding site to other structurally important regions of the spike. However, this study was conducted without considering the impact of glycans. It is now known that glycans play a crucial role in modulating spike dynamics. This new manuscript investigates how the presence of glycans affects the allosteric network connecting the lipid binding site to the rest of the spike. The authors conducted atomistic equilibrium and out-of-equilibrium MD simulations and found that while the presence of glycans influences the structural responses, it does not fundamentally alter the connectivity between the fatty acid site and the rest of the spike.

Strengths:

The manuscript's findings are based on an impressive amount of sampling. The methods and results are clearly outlined, and the analysis is conducted meticulously.

Author response:

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

Reviewer #1:

We thank the Reviewer for being very supportive of the work and acknowledging how important it is to understand allosteric modulation in the spike and the potential of this knowledge to contribute to the design of novel therapeutic strategies (for example, disrupting or altering the allosteric networks within the spike can be a novel strategy for drug development against COVID-19). We address their comments below: 

(1) The Reviewer states that although the strategy used to extract the responses has been "previously validated", the complexity of the interactions investigated requires "a robust statistical analysis, which is not shown quantitatively". 

As the Reviewer points out, the D-NEMD approach has been previously validated in various protein systems ranging from soluble enzymes to integral membrane proteins, including the spike (e.g. [Kamsri et al. (2024) Biochem; Beer et al. (2024) Chem Sci; Oliveira et al. (2023) J Mol Cell Biol; Chan et al. (2023) JACS Au; Castelli et al. (2023) JACS; Castelli et al. (2023) Protein Sci; Oliveira et al. (2022) Comput Struct Biotechnol J; Gupta et al. (2022) Nat Comm; Oliveira et al. (2021) JACS; Galdadas et al. (2021) eLife; Abreu et al. (2019) Proteins; Oliveira et al. (2019) JACS; Oliveira et al. (2019) Structure]. The Kubo-Onsager relation is used to extract the evolution of the protein's response to a perturbation by comparing the equilibrium and nonequilibrium trajectories at equivalent points in time. The calculated responses at individual times are then averaged over all the repeats (210 repeats in the current work), and the standard error of the mean (SEM) is used to assess the significance of the average response. The SEM indicates how much the calculated mean deviates from the true population mean. Calculating the SEM allows us to determine how accurate the measured response is as an estimate of the population response and assess the convergence of our calculations. The evolution of the average C_α displacement and corresponding SEM values for each individual monomer can be visualised in detail in Figures S7-S9. We have added a new sentence to the Materials and Methods section in the Supporting Information, explicitly stating how the convergence and statistical significance of the responses were assessed.

(2) The Reviewer considers that the evidence presented in the paper "is compelling" but suggests performing a sequence analysis to facilitate the understanding of the results by the scientific community. 

We thank the Reviewer for their excellent suggestion to perform a sequence analysis of the FA site region and its allosteric connections. Indeed, this analysis (Figure S24) clearly shows that several of the mutations, deletions and insertions in the Alpha, Beta, Gamma, Delta, and Omicron variants are located either in or near the regions of the protein shown to respond to the removal of linoleate from the FA site. These sequence changes affect the protein's responses, and are responsible for the differences in allosteric behaviour observed between variants, as described previously for the non-glycosylated spike [Oliveira et al. (2023) J Mol Cell Biol]. Furthermore, some variants, such as Beta, Gamma, and Omicron, contain residue substitutions at the FA site. For example, the lysine in position 417 in the ancestral spike is mutated to asparagine in Beta and Omicron and threonine in the Gamma variant. Another example is arginine 408 in the original protein, which has been replaced by asparagine in several Omicron sub-variants. 

To summarise, the sequence analysis (Figure S24) supports our initial 3D analysis (Figure S25), indicating that many of the changes observed in the variants of concern are indeed in or close to the allosteric networks involving the FA site. We have now included the sequence analysis results in the current paper and added a new figure to Supporting Information showing the sequence alignments between the ancestral spike and different variants (Figure S24). 

(3) The Reviewer also has "minor considerations": first, they point to a discrepancy in the presentation of residue values S325 in the plots of Chains A, B, and C of Figure S3; second, they ask why several regions, such as RBM and Furin Site in figures S6, S7, and S8 show significant changes.

To answer both points raised by the Reviewer, we need to start by explaining that the spike typically features 22 N-glycosylation and at least two O-glycans sites per monomer. These sites have been found to be heterogeneously populated in different experimental studies (e.g. [Watanabe et al. (2020) Science; Shajahan et al. (2020) Glycobiology; Zhang et al. (2021) Mol Cell Proteomics]). Given this, the spike model used as the starting point for this work reflects this heterogeneity, with asymmetric site-specific glycosylation profiles derived from the glycoanalytic data reported by Watanable et al. for N-glycans [Watanabe et al. (2020) Science] and Shajahan et al. for O-glycans [Shajahan et al. (2020) Glycobiology]. This means that the glycan occupancy and composition for each site differ between the three monomers. For example, while monomer A contains the two O-glycans sites (linked to T323 and S325, respectively) fully occupied, monomers B and C only contain the T323 O-glycan. A detailed description of the glycosylation of the spike model is given in the supporting information of [Casalino et al. (2020) ACS Cent Sci].

Regarding the Reviewer's first minor point, the discrepancy in behaviour observed in Figure S3 for S325 is related to the fact that this glycosylation site is only occupied in monomer A, with no glycans present in this site in monomers B and C. 

Regarding the second point, the differences observed in the responses between the three monomers in Figures S7-S9 are probably due to asymmetries in the protein dynamics introduced by the different glycosylation patterns in the monomers. 

We have now added a new paragraph to the materials and methods section in the Supporting Information describing the asymmetric site-specific glycosylation profiles of the monomers.

(4) Due to the complexity of the allosteric interactions observed, the Reviewer suggests including in the paper a "diagram showing the flow of allosteric interactions" or a "vector showing how the perturbation done in the FA Active site takes contact with other relevant regions". 

This is an excellent suggestion to facilitate the visualisation of the allosteric networks. We have added a new figure to Supporting Information highlighting the allosteric pathways identified from the DNEMD simulations and the direction of the propagation of the structural changes (Figure S26).

Reviewer #2:

We thank the Reviewer for their time in evaluating our manuscript and providing suggestions for improving it and ideas for further work. We are happy that the Reviewer found this to be a "nice paper" with the calculations "well done" and interesting results. We address their comments below: 

(1) The Reviewer suggests improving the paper by adding a more detailed explanation of the DNEMD simulations approach, a method that, although proposed decades ago, is still generally unfamiliar to the community. They also asked for "information on the convergence of the observables".

As stated by the Reviewer, a dynamical approach to nonequilibrium molecular dynamics (D-NEMD) was first proposed in the seventies by Ciccotti et al. [Ciccotti et al. (1975) Phys Rev Lett; Ciccotti et al. (1979) J Stat Phys]. This approach combines MD simulations in equilibrium and nonequilibrium conditions. The rationale for the D-NEMD approach is simple and can be described as follows: if an external perturbation (e.g. binding/unbinding of a ligand) is added to a simulation sampling an equilibrium state and, by doing so, a parallel nonequilibrium simulation is started, the structural response of the protein to the perturbation can be directly measured by comparing the equilibrium and nonequilibrium trajectories at equivalent points in time by using the Kubo-Onsager relation as long as enough sapling is gathered (for more details, please see the reviews [Balega et al. (2024) Mol Phys; Oliveira et al. (2021) Eur Phys J B; Ciccotti et al. (2016) Mol Simul]). This approach, although conceptually simple, is very powerful as it allows for computing the evolution of the dynamic response of the protein to the external perturbation, while assessing the convergence and statistical significance of that response. This approach also has the advantage that the convergence and significance of the response can be easily evaluated, and the associated errors can be computed and made as small as desirable by increasing the number of nonequilibrium trajectories. Determining the statistical errors associated with the responses (through, e.g., the determination of the standard error of the mean, SEM) is essential to test if the sampling gathered is sufficient. In this paper, the SEM was calculated for each average C_α displacement value at times 0.1, 1 and 10 ns after the removal of linoleate, LA (see Figures S7-S9). The SEM indicates how accurate the measured response is as an estimate of the population response and allows us to assess the convergence of the results. 

Generally, multiple (tens to hundreds) D-NEMD simulations are needed to achieve statistically significant results for biomolecular systems (for examples, see [Balega et al. (2024) Mol Phys; Oliveira et al. (2021) Eur Phys J B]). As such, the length of the D-NEMD simulations (typically 5 to 10 ns) reflects the balance between the computational resources available and the number of replicates needed to achieve statistically significant responses from the system. Following the Reviewer's suggestion, we have now added a brief description of the D-NEMD approach to the main manuscript and expanded the D-NEMD section in the Supporting Information with a more detailed description of the method, including adding a new figure showing a schematic representation of the D-NEMD approach (Figure S5) as well as explicitly stating the settings used in these simulations and how the statistical significance of the responses was assessed. 

(2) The Reviewer suggests comparing the D-NEMD results with "more traditional analysis, such as correlation analysis, or community network analysis". 

We agree with the Reviewer that this is an important comparison, which can provide a broader, more articulate and coherent picture of spike allostery and have, therefore, performed additional analysis. The dynamic cross-correlation analysis suggested by the Reviewer is a valuable tool for identifying the regions in the protein influenced by the FA site in equilibrium conditions. However, such an approach is not straightforwardly applicable to D-NEMD simulations, as these simulations are not in equilibrium. Nevertheless, as suggested by the Reviewer, we have determined the cross-correlation matrices for both the equilibrium and D-NEMD simulations (Figure S22), similar to those in our previous work [Galdadas et al. (2021) eLife] and [Oliveira et al. (2022) J Mol Cell Biol]. The analysis of these matrices can provide information about possible allosteric networks. In Figure S22, the cyan and blue regions represent moderate and high negative correlations between C_α atoms, while orange and red regions correspond to moderate and high positive correlations. Negative correlations indicate residues moving in opposite directions (moving toward or away from each other). In contrast, positive values imply that the residues are moving in similar directions. We also note that, with collaborators, we have compared D-NEMD and other nonequilibrium and equilibrium MD analysis methods for allostery [Castelli et al.  (2023) JACS].

The cross-correlation maps depicted in Figure S22 show moderate to high positive correlations between the FA sites and two of the three RBDs in the protein. This happens because each FA site sits at the interface between two neighbouring RBDs. Low to moderate negative and mildly positive correlated motions can also be observed between the FA site and the NTDs and fusion peptide surrounding regions, respectively. To facilitate the visualisation of the above-described motions, we have also mapped the statistical correlations for R408 and K417 (two FA site residues able to directly form salt-bridge interactions with the carboxylate head group of LA) on the protein's three-dimensional structure (Figure S23). Figure S23 highlights the patterns of movement described above and allows us to identify the regions whose motions are coupled to the FA site.

Interestingly, some segments forming the signal propagation pathways, such as R454-K458 in all three monomers, and C525-K537 in monomers B and C, can also be identified from the cross-correlation matrices, showing moderate to high correlations with the FA site (Figures S22-S23). The crosscorrelation maps computed from the equilibrium trajectories (with FA sites occupied with LA) show a slight increase in the dynamic correlations, mainly for the RBDs, compared to the maps obtained from the nonequilibrium trajectories (Figure S22). This indicates that the presence of LA in the FA strengthens the connections between the FA site and other parts of the protein. 

We have updated the manuscript to include the cross-correlation analysis, with two new figures added to Supporting Information: one depicting the cross-correlation maps for the D-NEMD and equilibrium simulations (Figure S22), and the other showing the statistical correlations for R408 and K417 (Figure S23). 

(3) The Reviewer considers the observed connection between the fatty acid site and the heme/biliverdin site "interesting" and suggests "exploring the impact of ligand removal on this secondary site on the protein".

Similarly to the Reviewer, we find the connection between the FA and the heme/biliverdin site fascinating and worthy of further investigation. The observed connection between these two sites shows the complexity of the allosteric effects in the spike. It would be interesting and informative to perform new equilibrium simulations of the heme/biliverdin spike complex and a new set of D-NEMD simulations in which this site is perturbed (e.g. through the removal of the heme group) to map the networks connecting this allosteric site to other functionally important regions of the spike, including the FA site and potentially other allosteric sites. These new simulations would allow us to assess the reversibility of the connection between the FA and heme/biliverdin sites and enhance our understanding of allosteric modulation in the spike and the role of the heme/biliverdin site in this process. However, due to the large size of the system and the associated computational demands, such simulations are not possible within the timeframe of the revision of this paper. These simulations would take many months to complete using our HPC resources. We also note that an experimental structure of the spike containing both heme and linoleate is not available. Further simulation analysis of the communication pathways involving the heme/biliverdin site is an excellent idea for future work.

(4) The Reviewer "liked the mapping of existing mutations on the communication pathway" and suggested a more detailed study focusing on the effect of the mutations. 

We fully agree with the Reviewer and consider that a detailed study focusing on the effect of the mutations, insertions, and deletions in the different glycosylated variants of concern (including new emerging ones) would be of great interest. Our previous work using D-NEMD on the non-glycosylated ancestral, Alpha, Delta, Delta plus and Omicron BA.1 spikes revealed significant differences in the allosteric responses to LA removal, with the changes in the variants affecting both the amplitude of the structural responses and the rates at which these rearrangements propagate within the protein [Oliveira et al. (2023) J Mol Cell Biol]. 

Using the D-NEMD approach to systematically investigate the impact of each individual mutation and their contribution to the overall allosteric response of the glycosylated variants (similar to what we have done previously for the D614G mutation in the non-glycosylated protein [Oliveira et al. (2021) Comput Struct Biotechnol J]) would provide insights into the functional modulation of the spike. However, as noted above in point 3, spike simulations are highly computationally expensive, both in terms of processing and data storage requirements, because of the large size of the protein and the need for equilibrium and D-NEMD simulations. This makes the suggested mutational study unfeasible within the timeframe of the current revisions. It is, however, an excellent idea for future research.

Reviewer #3:

We thank the Reviewer for carefully reading and critically reviewing this work and recognising that the findings reported are "based on an impressive amount of sampling" and "meticulous" analysis. We address their comments below: 

(1) The Reviewer considers that this work "does not clearly show any new findings" as it shows that the glycans do not significantly impact the internal networks in the protein.

We respectfully disagree with the Reviewer. This work identifies new allosteric effects in the spike, specifically, the connection of the FA site with the heme binding site. The equilibrium simulations alone provide the first analysis of the effects of linoleate binding in the fully glycosylated spike. The finding that glycosylation does not significantly affect the allosteric pathways in the spike is in itself an important finding. Previous D-NEMD simulations investigated only the non-glycosylated spike ([Oliveira et al. (2021) Comput Struct Biotechnol J; Oliveira et al. (2022) J Mol Cell Biol] ) leading to questions of whether the allosteric effects pathways were changed by glycosylation; our results here show that the main conclusions are reinforced, but glycosylation does have some effect on networks, and also on the speed of the dynamical response. To the best of our knowledge, our work represents the first investigation to analyse the impact of glycosylation on the allosteric networks in the spike. We show that even though the presence of glycans in the exterior of the spike does not significantly alter the internal communication pathways in the protein, in some cases (for example, the glycans linked to N234, T373 and S375), they create direct connections between different regions, which may facilitate the propagation of the structural changes. 

(2) The Reviewer suggests adding a "clear and concise description" of the D-NEMD approach to the manuscript.

We appreciate that the use of the D-NEMD method to study biomolecular systems is relatively new, and so may be unfamiliar. As explained above in our response to Reviewer 2 (point 1), a brief description of the D-NEMD approach was now included in the main manuscript. A detailed description of the method was also added to Supporting Information, including a new figure representing the rationale for the approach (Figure S5). The interested reader is directed to previous applications and reviews for more details of the method (e.g. [Balega et al. (2024) Mol Phys; Oliveira et al. (2021) Eur Phys J B; Ciccotti et al. (2016) Mol Simul; Kamsri et al. (2024) Biochem; Beer et al. (2024) Chem Sci; Oliveira et al. (2023) J Mol Cell Biol; Chan et al. (2023) JACS Au; Castelli et al. (2023) JACS; Castelli et al. (2023) Protein Sci; Oliveira et al. (2022) Comput Struct Biotechnol J; Gupta et al. (2022) Nat Comm; Oliveira et al. (2021) JACS; Galdadas et al. (2021) eLife; Abreu et al. (2019) Proteins; Oliveira et al. (2019) JACS; Oliveira et al. (2019) Structure]). 

(3) The Reviewer invites us to "discuss the robustness of the findings with respect to forcefield choices".

The Reviewer raises an important but rather complex question, and one which can, of course, be posed for any molecular dynamics simulation study. The short answer is that we have chosen state-of-the-art forcefields, which have been shown to give results for the spike that are in good agreement with experiments; glycosylated spike simulations are rather computationally expensive, and constructing the models also requires significant human time and effort. Thus, while in principle interesting, it is not practical to repeat the current simulations with different forcefields. However, as detailed below, comparison of our simulations of the glycosylated and non-glycosylated [Oliveira et al. (2022) Comput Struct Biotechnol J] spike using different forcefields indicates that our conclusions are robust and are not dependent on the choice of forcefield. 

Comparing the performance and accuracy of different force fields is not straightforward, as the results depend on the system of interest, properties simulated and sampling. In this work, the CHARMM36m all-atom additive force field was used to describe the protein and glycans. CHARMM36m is a widely used force field that has previously been validated for the simulations of biological systems [Huang et al. (2013) J Comput Chem; Guvench et al. (2009) J Chem Theory Comput], including proteins, lipids and glycans, with many of studies adopting it in the literature. Additionally, the glycosylated models of the spike used in this work have also been successfully applied and tested before (e.g. [Dommer et al. (2023) Int J High Perform Comput Appl; Sztain et al. (2021) Nat Chem; Casalino et al. (2021) Int J High Perform Comput Appl; Casalino et al. (2020) ACS Cent Sci]), with their dynamics shown to correlate well with experimental data.   

It is also worth pointing out that, despite differences in the amplitude of the responses, the allosteric networks identified using the D-NEMD approach for the non-glycosylated [Oliveira et al. (2022) Comput Struct Biotechnol J] and glycosylated spikes are generally similar (Figure S13). While the responses for the non-glycosylated protein were extracted from simulations using the AMBER99SBILDN forcefield [Oliveira et al. (2022) Comput Struct Biotechnol J], those reported in this work were obtained from trajectories using the CHARMM36m forcefield. The similarity between the responses for the two systems (which were simulated using different forcefields) is a good indication that our findings are forcefield independent. 

(4) The Reviewer suggests comparing our findings with "alternative methods of analysing allostery". 

As stated above in our response to Reviewer 2 point 2, we consider the suggested comparison an excellent idea. We have therefore performed a dynamic cross-correlation analysis to identify the regions in the protein coupled to the FA site in both equilibrium and nonequilibrium conditions (see Figures S22-S23). Overall, this analysis shows that the FA site motions are strongly coupled to the RBDs and moderately to weakly connected to the NTDs and fusion peptide surrounding regions (please see a detailed description of the results of the correlation analysis in our response to Reviewer 2 point 2). The cross-correlation analysis performed was added to the manuscript, and two new figures were included in the Supporting Information (Figures S22-S23): the first, showing the cross-correlation maps for the D-NEMD and equilibrium simulations; the second, showing the statistical correlations for R408 and K417 (two residues forming the FA site and that can directly interact with the carboxylate head group of LA). 

We agree that comparing different allosteric analysis methods is interesting, informative and important. As noted above, we have compared D-NEMD and other nonequilibrium and equilibrium MD analysis methods for allostery in the well-characterised K-Ras system [Castelli et al.  (2023) JACS].

eLife Assessment

In this manuscript, Abd El Hay and colleagues use an innovative behavioral assay and analysis method, together with standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons, to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. Compelling evidence is provided for a role of TRPM2 channels in warmth avoidance behavior, but it remains unclear whether this involves channel activity in the periphery or in the brain. In contrast, TRPV1 is clearly implicated at the cellular level in warmth detection. These findings are important because there is substantial ongoing discussion regarding the contribution of TRP channels to different aspects of thermo-sensation.

Reviewer #3 (Public review):

A central question in the thermal system is which thermally responsive ion channels are responsible for warm evoked behaviors and DRG afferent neuron responses to warming. Recent work has shown evidence for TRPV1, TRPM2 and TRPM8. Here Abd El Hay and colleagues investigate the role of TRPM2 and TRPV1 in a novel warm preference behavior and in the thermal responses of cultured DRG neurons.

They develop a new thermal preference task, where both the floor and air temperature are controlled, which shows differences to the classic two-plate preference task. This is a central strength of the paper, as it will allow a new method to investigate how animals integrating floor and air temperature. They go on to use knockout mice and confirm a clear role for TRPM2 in warm preference behavior.

Using a new approach for culturing DRG neurons they investigate the involvement of both channels in warm responsiveness and dynamics. In apparent contrast to the role of TRPM2 on thermal behavior, it does not have a major effect on the responses of cultured DRG neurons to warm stimuli. Eliminating TRPV1 however has a stronger impact on DRG responses, particularly at low stimulus amplitudes. It will be important to discover how TRPM2 influences warm driven behaviors, if it is not via changes in afferent response properties.

Thanks to the authors for addressing my remaining questions in this updated version of the manuscript.

This is an interesting study with novel approaches that generates new information on the differing roles of TRPV1 and TRPM2 on thermal behavior.

Author response:

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

Public Reviews:  

Reviewer # 1 (Public Review): 

Summary:

The authors use an innovative behavior assay (chamber preference test) and standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. They find a profound effect of TRPM2 elimination in the behavioral assay, whereas the elimination of TRPV1 has the largest effect on the neuronal responses. These findings are very important, as there is substantial ongoing discussion in the field regarding the contribution of TRP channels to different aspects of thermosensation.

Strengths:

The chamber preference test is an important innovation compared to the standard two-plate test, as it depends on thermal information sampled from the entire skin, as opposed to only the plantar side of the paws. With this assay, and the detailed analysis, the authors provide strong supporting evidence for a role of TRPM2 in warmth avoidance. The conceptual framework using the Drift Diffusion Model provides a first glimpse of how this decision of a mouse to change between temperatures can be interpreted and may form the basis for further analysis of thermosensory behavior.

Weaknesses:

The authors juxtapose these behavioral data with calcium imaging data using isolated DRG neurons. As the authors acknowledge, it remains unclear whether the clear behavioral effect seen in the TRPM2 knockout animals is directly related to TRPM2 functioning as a warmth sensor in sensory neurons. The effects of the TRPM2 KO on the proportion of warmth sensing neurons are very subtle, and TRPM2 may also play a role in the behavioral assay through its expression in thermoregulatory processes in the brain. Future behavioral experiments on sensory-neuron specific TRPM2 knockout animals will be required to clarify this important point.

Reviewer # 1 (Recommendations for the authors):

(1) I have no further suggestions for the authors, and congratulate them with their excellent study.

For the authors information, ref. 42 does contain behavioral data from both male (Fig. 4 and Extended Figure 7) and female (Extended Figure 8) mice.

We thank the referee for pointing out that both males and female mice were tested in the Vandewauw et al. 2018 study. We deliberated whether to include this at the appropriate section of our manuscript (“Limitations of the Study”). But since Vandewauw et al. assessed noxious heat temperatures and we here assess innocuous warmth temperature, we felt that this reference would not add to the clarification whether there are sex differences in Trp channelbased warmth temperature sensing. In particular, we did not want to “use” the argument and to suggest that there are no sex temperature differences in the warmth range just because Vandewauw et al. did not observe major sex differences in the noxious temperature range. 

Reviewer #3 (Public Review):  

Summary and strengths:

In the manuscript, Abd El Hay et al investigate the role of thermally sensitive ion channels TRPM2 and TRPV1 in warm preference and their dynamic response features to thermal stimulation. They develop a novel thermal preference task, where both the floor and air temperature are controlled, and conclude that mice likely integrate floor with air temperature to form a thermal preference. They go on to use knockout mice and show that TRPM2-/- mice play a role in the avoidance of warmer temperatures. Using a new approach for culturing DRG neurons they show the involvement of both channels in warm responsiveness and dynamics. This is an interesting study with novel methods that generate important new information on the different roles of TRPV1 and TRPM2 on thermal behavior.

Comments on revisions:

Thanks to the authors for addressing all the points raised. They now include more details about the classifier, better place their work in context of the literature, corrected the FOVs, and explained the model a bit further. The new analysis in Figure 2 has thrown up some surprising results about cellular responses that seem to reduce the connection between the cellular and behavioral data and there are a few things to address because of this:

(1) TRPM2 deficient responses: The differences in the proportion of TRPM2 deficient responders compared to WT are only observed at one amplitude (39C), and even at this amplitude the effect is subtle. Most surprisingly, TRPM2 deficient cells have an enhanced response to warm compared to WT mice to 33C, but the same response amplitude as WT at 36C and 39C. The authors discuss why this disconnect might be the case, but together with the lack of differences between WT and TRPM2 deficient mice in Fig 3, the data seem in good agreement with ref 7 that there is little effect of TRPM2 on DRG responses to warm in contrast to a larger effect of TRPV1. This doesn't take away from the fact there is a behavioral phenotype in the TRPM2 deficient mice, but the impact of TRPM2 on DRG cellular warm responses is weak and the authors should tone down or remove statements about the strength of TRPM2's impact throughout the manuscript, for example:

"Trpv1 and Trpm2 knockouts have decreased proportions of WSNs."

"this is the first cellular evidence for the involvement of TRPM2 on the response of DRG sensory neurons to warm-temperature stimuli"

"we demonstrate that TRPV1 and TRPM2 channels contribute differently to temperature detection, supported by behavioural and cellular data"

"TRPV1 and TRPM2 affect the abundance of WSNs, with TRPV1 mediating the rapid, dynamic response to warmth and TRPM2 affecting the population response of WSNs."

"Lack of TRPV1 or TRPM2 led to a significant reduction in the proportion of WSNs, compared to wildtype cultures".

We agree with the referee that the somewhat surprising result of the subtle phenotype in Trpm2 knock-out DRG culture experiments, that became detectable in the course of the new analysis, was overemphasized in the previous version of the manuscript. Per suggestion, we have toned down or removed the statements in the revised manuscript (for the referee to find those changes easily, they are indicated in “track-changes mode” in the submitted document).  

(2) The new analysis also shows that the removal of TRPV1 leads to cellular responses with smaller responses at low stimulus levels but larger responses with longer latencies at higher stimulus levels. Authors should discuss this further and how it fits with the behavioral data.

Because these changes shown in Fig. 2E are also subtle (similar to the cellular Trpm2 phenotype discussed above), and because both the “% Responders” (Fig 2.D) and The AUC analysis (Fig. 2F) show a reduction in Trpv1 knock out cultures ––both, at lower and at higher stimulus levels–– we did not want to overstate this difference too much and therefore did not further discuss this aspect in the context of the behavioral differences observed in the Trpv1 knock-out animals.  

(3) Analysis clarification: authors state that TRPM2 deficient WSNs show "Their response to the second and third stimulus, however, are similar to wildtype WSNs, suggesting that tuning of the response magnitude to different warmth stimuli is degraded in Trpm2-/- animals." but is there a graded response in WT mice? It looks like there is in terms of the %responders but not in terms of response amplitude or AUC. Authors could show stats on the figure showing differences in response amplitude/AUC/responders% to different stimulus amplitudes within the WT group.

We have added the statistics in the main text, you find them on page 7 (also in “track changes mode”).

(4) New discussion point: sex differences are "similar to what has been shown for an operant-based thermal choice assay (11,56)", but in their rebuttal, they mention that ref 11 did not report sex differences. 56 does. Check this.

Thank you for pointing out this mishap. We have now corrected this in the “Limitations of the study” section of the discussion and have removed the Paricio-Montesions et al study from that section and slightly revised the text (see “track-changes” on page 16).

(5) The authors added in new text about the drift diffusion model in the results, however it's still not completely clear whether the "noise" is due to a perceptual deficit or some other underlying cause. Perhaps authors could discuss this further in the discussion.

We have now included more discussion concerning this (page 14):

“However, the increased noise in the drift-di3usion model points to a less reliable temperature detection mechanism. Although noise in drift di3usion models can encompass various sources of variability—ranging from peripheral sensory processing to central mechanisms like attention or motor initiation—the most parsimonious interpretation in our study aligns with a perceptual deficit, given the altered temperatureresponsive neuronal populations we observed. This implies that, despite the substantial loss of WSNs, the remaining neuronal population provides su3icient information for the detection of warmer temperatures, albeit with reduced precision”

Within the limits of the data that is available, we hope the referee agrees with us that we have now adequately discussed this aspect; we feel that any further discussion would be too speculative.