Author response:

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

Reviewer #1 (Public review):

Summary:

The paper presents a model for sequence generation in the zebra finch HVC, which adheres to cellular properties measured experimentally. However, the model is fine-tuned and exhibits limited robustness to noise inherent in the inhibitory interneurons within the HVC, as well as to fluctuations in connectivity between neurons. Although the proposed microcircuits are introduced as units for sub-syllabic segments (SSS), the backbone of the network remains a feedforward chain of HVC_RA neurons, similar to previous models.

Strengths:

The model incorporates all three of the major types of HVC neurons. The ion channels used and their kinetics are based on experimental measurements. The connection patterns of the neurons are also constrained by the experiments.

Weaknesses:

The model is described as consisting of micro-circuits corresponding to SSS. This presentation gives the impression that the model's structure is distinct from previous models, which connected HVC_RA neurons in feedforward chain networks (Jin et al 2007, Li & Greenside, 2006; Long et al 2010; Egger et al 2020). However, the authors implement single HVC_RA neurons into chain networks within each micro-circuit and then connect the end of the chain to the start of the chain in the subsequent micro-circuit. Thus, the HVC_RA neuron in their model forms a single-neuron chain. This structure is essentially a simplified version of earlier models.

In the model of the paper, the chain network drives the HVC_I and HVC_X neurons. The role of the micro-circuits is more significant in organizing the connections: specifically, from HVC_RA neurons to HVC_I neurons, and from HVC_I neurons to both HVC_X and HVC_RA neurons.

We thank Reviewer 1 for their thoughtful comments.

While the reviewer is correct about the fact that the propagation of sequential activity in this model is primarily carried by HVC_RA neurons in a feed-forward manner, we need to emphasize that this is true only if there is no intrinsic or synaptic perturbation to the HVC network. For example, we showed in Figures 10 and 12 how altering the intrinsic properties of HVC_X neurons or for interneurons disrupts sequence propagation. In other words, while HVC_RA neurons are the key forces to carry the chain forward, the interplay between excitation and inhibition in our network as well as the intrinsic parameters for all classes of HVC neurons are equally important forces in carrying the chain of activity forward. Thus, the stability of activity propagation necessary for song production depend on a finely balanced network of HVC neurons, with all classes contributing to the overall dynamics. Moreover, all existing models that describe premotor sequence generation in the HVC either assume a distributed model (Elmaleh et al., 2021) that dictates that local HVC circuitry is not sufficient to advance the sequence but rather depends upon moment to-moment feedback through Uva (Hamaguchi et al., 2016), or assume models that rely on intrinsic connections within HVC to propagate sequential activity. In the latter case, some models assume that HVC is composed of multiple discrete subnetworks that encode individual song elements (Glaze & Troyer, 2013; Long & Fee, 2008; Wang et al., 2008), but lacks the local connectivity to link the subnetworks, while other models assume that HVC may have sufficient information in its intrinsic connections to form a single continuous network sequence (Long et al. 2010). The HVC model we present extends the concept of a feedforward network by incorporating additional neuronal classes that influence the propagation of activity (interneurons and HVC_X neurons). We have shown that any disturbance of the intrinsic or synaptic conductances of these latter neurons will disrupt activity in the circuit even when HVC_RA neurons properties are maintained. 

In regard to the similarities between our model and earlier models, several aspects of our model distinguish it from prior work. In short, while several models of how sequence is generated within HVC have been proposed (Cannon et al., 2015; Drew & Abbott, 2003; Egger et al., 2020; Elmaleh et al., 2021; Galvis et al., 2018; Gibb et al., 2009a, 2009b; Hamaguchi et al., 2016; Jin, 2009; Long & Fee, 2008; Markowitz et al., 2015), all the models proposed either rely on intrinsic HVC circuitry to propagate sequential activity, rely on extrinsic feedback to advance the sequence or rely on both. These models do not capture the complex details of spike morphology, do not include the right ionic currents, do not incorporate all classes of HVC neurons, or do not generate realistic firing patterns as seen in vivo. Our model is the first biophysically realistic model that incorporates all classes of HVC neurons and their intrinsic properties. We tuned the intrinsic and the synaptic properties bases on the traces collected by Daou et al. (2013) and Mooney and Prather (2005) as shown in Figure 3. The three classes of model neurons incorporated to our network as well as the synaptic currents that connect them are based on Hodgkin- Huxley formalisms that contain ion channels and synaptic currents which had been pharmacologically identified. This is an advancement over prior models that primarily focused on the role of synaptic interactions or external inputs. The model is based on feedforward chain of microcircuits that encode for the different sub-syllabic segments and that interact with each other through structured feedback inhibition, defining an ordered sequence of cell firing. Moreover, while several models highlight the critical role of inhibitory interneurons in shaping the timing and propagation of bursts of activity in HVC_RA neurons, our work offers an intricate and comprehensive model that help understand this critical role played by inhibition in shaping song dynamics and ensuring sequence propagation.

How useful is this concept of micro-circuits? HVC neurons fire continuously even during the silent gaps. There are no SSS during these silent gaps.

Regarding the concern about the usefulness of the 'microcircuit' concept in our study, we appreciate the comment and we are glad to clarify its relevance in our network. While we acknowledge that HVC_RA neurons interconnect microcircuits, our model's dynamics are still best described within the framework of microcircuitry particularly due to the firing behavior of HVC_X neurons and interneurons. Here, we are referring to microcircuits in a more functional sense, rather than rigid, isolated spatial divisions (Cannon et al. 2015), and we now make this clear on page 21. A microcircuit in our model reflects the local rules that govern the interaction between all HVC neuron classes within the broader network, and that are essential for proper activity propagation. For example, HVC_INT neurons belonging to any microcircuit burst densely and at times other than the moments when the corresponding encoded SSS is being “sung”. What makes a particular interneuron belong to this microcircuit or the other is merely the fact that it cannot inhibit HVC_RA neurons that are housed in the microcircuit it belongs to. In particular, if HVC_INT inhibits HVC_RA in the same microcircuit, some of the HVC_RA bursts in the microcircuit might be silenced by the dense and strong HVC_INT inhibition breaking the chain of activity again. Similarly, HVC_X neurons were selected to be housed within microcircuits due to the following reason: if an HVC_X neuron belonging to microcircuit i sends excitatory input to an HVC_INT neuron in microcircuit j, and that interneuron happens to select an HVC_RA neuron from microcircuit i, then the propagation of sequential activity will halt, and we’ll be in a scenario similar to what was described earlier for HVC_INT neurons inhibiting HVC_RA neurons in the same microcircuit.

We agree that there are no sub-syllabic segments described during the silent gaps and we thank the reviewer to pointing this out. Although silent gaps are integral to the overall process of song production, we have not elaborated on them in this model due to the lack of a clear, biophysically grounded representation for the gaps themselves at the level of HVC. Our primary focus has been on modeling the active, syllable-producing phases of the song, where the HVC network’s sequential dynamics are critical for song. However, one can think the encoding of silent gaps via similar mechanisms that encode SSSs, where each gap is encoded by similar microcircuits comprised of the three classes of HVC neurons (let’s call them GAP rather than SSS) that are active only during the silent gaps. In this case, the propagation of sequential activity is carried throughout the GAPs from the last SSS of the previous syllable to the first SSS of the subsequent syllable. This is no described more clearly on page 22 of the manuscript.

A significant issue of the current model is that the HVC_RA to HVC_RA connections require fine-tuning, with the network functioning only within a narrow range of g_AMPA (Figure 2B). Similarly, the connections from HVC_I neurons to HVC_RA neurons also require fine-tuning. This sensitivity arises because the somatic properties of HVC_RA neurons are insufficient to produce the stereotypical bursts of spikes observed in recordings from singing birds, as demonstrated in previous studies (Jin et al 2007; Long et al 2010). In these previous works, to address this limitation, a dendritic spike mechanism was introduced to generate an intrinsic bursting capability, which is absent in the somatic compartment of HVC_RA neurons. This dendritic mechanism significantly enhances the robustness of the chain network, eliminating the need to fine-tune any synaptic conductances, including those from HVC_I neurons (Long et al 2010). Why is it important that the model should NOT be sensitive to the connection strengths?

We thank the reviewer for the comment. While mathematical models designed for highly complex nonlinear biological processes tangentially touch the biological realism, the current network as is right now is the first biologically realistic-enough network model designed for HVC that explains sequence propagation. We do not include dendritic processes in our network although that increases the realistic dynamics for various reasons. 1) The ion channels we integrated into the somatic compartment are known pharmacologically (Daou et al. 2013), but we don’t know about the dendritic compartment’s intrinsic properties of HVC neurons and the cocktail of ion channels that are expressed there. 2) We are able to generate realistic bursting in HVC_RA neurons despite the single compartment, and the main emphasis in this network is on the interactions between excitation and inhibition, the effects of ion channels in modulating sequence propagation, etc … 3) The network model already incorporates thousands of ODEs that govern the dynamics of each of the HVC neurons, so we did not want to add more complexity to the network especially that we don’t know the biophysical properties of the dendritic compartments.

Therefore, our present focus is on somatic dynamics and the interaction between HVC_RA and HVC_INT neurons, but we acknowledge the importance of these processes in enhancing network resiliency. Although we agree that adding dendritic processes improves robustness, we still think that somatic processes alone can offer insightful information on the sequential dynamics of the HVC network. While the network should be robust across a wide range of parameters, it is also essential that certain parameters are designed to filter out weaker signals, ensuring that only reliable, precise patterns of activity propagate. Hence, we specifically chose to make the HVC_RA-to-HVC_RA excitatory connections more sensitive (narrow range of values) such that only strong, precise and meaningful stimuli can propagate through the network representing the high stereotypy and precision seen in song production.

First, the firing of HVC_I neurons is highly noisy and unreliable. HVC_I neurons fire spontaneous, random spikes under baseline conditions. During singing, their spike timing is imprecise and can vary significantly from trial to trial, with spikes appearing or disappearing across different trials. As a result, their inputs to HVC_RA neurons are inherently noisy. If the model relies on precisely tuned inputs from HVC_I neurons, the natural fluctuations in HVC_I firing would render the model non-functional. The authors should incorporate noisy HVC_I neurons into their model to evaluate whether this noise would render the model non-functional.

We acknowledge that under baseline and singing settings, interneurons fire in an extremely noisy and inaccurate manner, although they exhibit time locked episodes in their activity (Hahnloser et al 2002, Kozhinikov and Fee 2007). In order to mimic the biological variability of these neurons, our model does, in fact, include a stochastic current to reflect the intrinsic noise and random variations in interneuron firing shown in vivo (and we highlight this in the Methods). However, to make sure the network is resilient to this randomness in interneuron firing, introduced a stochastic input current of the form I_noise (t)= σ.ξ(t) where ξ(t) is a Gaussian white noise with zero mean and unit variance, and σ is the noise amplitude. This stochastic drive was introduced to every model neuron and it mimics the fluctuations in synaptic input arising from random presynaptic activity and background noise. For values of σ within 1-5% of the mean synaptic conductance, the stochastic current has no effect on network propagation. For larger values of σ, the desired network activity was disrupted or halted. We now talk about this on page 22 of the manuscript.  

Second, Kosche et al. (2015) demonstrated that reducing inhibition by suppressing HVC_I neuron activity makes HVC_RA firing less sparse but does not compromise the temporal precision of the bursts. In this experiment, the local application of gabazine should have severely disrupted HVC_I activity. However, it did not affect the timing precision of HVC_RA neuron firing, emphasizing the robustness of the HVC timing circuit. This robustness is inconsistent with the predictions of the current model, which depends on finely tuned inputs and should, therefore, be vulnerable to such disruptions.

We thank the reviewer for the comment. The differences between the Kosche et al. (2015) findings and the predictions of our model arise from differences in the aspect of HVC function we are modeling. Our model is more sensitive to inhibition, which is a designed mechanism for achieving precise song patterning. This is a modeling simplification we adopted to capture specific characteristics of HVC function. Hence, Kosche et al. (2015) findings do not invalidate the approach of our model, but highlights that HVC likely operates with several, redundant mechanisms that overall ensure temporal precision. 

Third, the reliance on fine-tuning of HVC_RA connections becomes problematic if the model is scaled up to include groups of HVC_RA neurons forming a chain network, rather than the single HVC_RA neurons used in the current work. With groups of HVC_RA neurons, the summation of presynaptic inputs to each HVC_RA neuron would need to be precisely maintained for the model to function. However, experimental evidence shows that the HVC circuit remains functional despite perturbations, such as a few degrees of cooling, micro-lesions, or turnover of HVC_RA neurons. Such robustness cannot be accounted for by a model that depends on finely tuned connections, as seen in the current implementation.

Our model of individual HVC_RA neurons and as stated previously is reductive model that focuses on understanding the mechanisms that govern sequential neural activity. We agree that scaling the model to include many of HVC_RA neurons poses challenges, specifically concerning the summation of presynaptic inputs. However, our model can still be adapted to a larger network without requiring the level of fine-tuning currently needed. In fact, the current fine-tuning of synaptic connections in the model is a reflection of fundamental network mechanisms rather than a limitation when scaling to a larger network. Besides, one important feature of this neural network is redundancy. Even if some neurons or synaptic connections are impaired, other neurons or pathways can compensate for these changes, allowing the activity propagation to remain intact.

The authors examined how altering the channel properties of neurons affects the activity in their model. While this approach is valid, many of the observed effects may stem from the delicate balancing required in their model for proper function. In the current model, HVC_X neurons burst as a result of rebound activity driven by the I_H current. Rebound bursts mediated by the I_H current typically require a highly hyperpolarized membrane potential. However, this mechanism would fail if the reversal potential of inhibition is higher than the required level of hyperpolarization. Furthermore, Mooney (2000) demonstrated that depolarizing the membrane potential of HVC_X neurons did not prevent bursts of these neurons during forward playback of the bird's own song, suggesting that these bursts (at least under anesthesia, which may be a different state altogether) are not necessarily caused by rebound activity. This discrepancy should be addressed or considered in the model.

In our HVC network model, one goal with HVC_X neurons is to generate bursts in their underlying neuron population. Since HVC_X neurons in our model receive only inhibitory inputs from interneurons, we rely on inhibition followed by rebound bursts orchestrated by the I_H and the I_CaT currents to achieve this goal. The interplay between the T-type Ca⁺⁺ current and the H current in our model is fundamental to generate their corresponding bursts, as they are sufficient for producing the desired behavior in the network. Due to this interplay, we do not need significant inhibition to generate rebound bursts, because the T-type Ca₊₊ current’s conductance can be stronger leading to robust rebound bursting even when the degree of inhibition is not very strong. This is now highlighted on page 42 in the revised version.

Some figures contain direct copies of figures from published papers. It is perhaps a better practice to replace them with schematics if possible.

We wanted on purpose to keep the results shown in Mooney and Prather (2005) to be shown as is, in order to compare them with our model simulations highlighting the degree of resemblance. We believe that creating schematics of the Mooney and Prather (2005) results will not have the same impact, similarly creating a schematic for Hahnloser et al (2002) results won’t help much. However, if the reviewer still believes that we should do that, we’re happy to do it.

Reviewer #2 (Public review):

Summary:

In this paper, the authors use numerical simulations to try to understand better a major experimental discovery in songbird neuroscience from 2002 by Richard Hahnloser and collaborators. The 2002 paper found that a certain class of projection neurons in the premotor nucleus HVC of adult male zebra finch songbirds, the neurons that project to another premotor nucleus RA, fired sparsely (once per song motif) and precisely (to about 1 ms accuracy) during singing.

The experimental discovery is important to understand since it initially suggested that the sparsely firing RA-projecting neurons acted as a simple clock that was localized to HVC and that controlled all details of the temporal hierarchy of singing: notes, syllables, gaps, and motifs. Later experiments suggested that the initial interpretation might be incomplete: that the temporal structure of adult male zebra finch songs instead emerged in a more complicated and distributed way, still not well understood, from the interaction of HVC with multiple other nuclei, including auditory and brainstem areas. So at least two major questions remain unanswered more than two decades after the 2002 experiment: What is the neurobiological mechanism that produces the sparse precise bursting: is it a local circuit in HVC or is it some combination of external input to HVC and local circuitry? And how is the sparse precise bursting in HVC related to a songbird's vocalizations? The authors only investigate part of the first question, whether the mechanism for sparse precise bursts is local to HVC. They do so indirectly, by using conductance-based Hodgkin-Huxley-like equations to simulate the spiking dynamics of a simplified network that includes three known major classes of HVC neurons and such that all neurons within a class are assumed to be identical. A strength of the calculations is that the authors include known biophysically deduced details of the different conductances of the three major classes of HVC neurons, and they take into account what is known, based on sparse paired recordings in slices, about how the three classes connect to one another. One weakness of the paper is that the authors make arbitrary and not well-motivated assumptions about the network geometry, and they do not use the flexibility of their simulations to study how their results depend on their network assumptions. A second weakness is that they ignore many known experimental details such as projections into HVC from other nuclei, dendritic computations (the somas and dendrites are treated by the authors as point-like isopotential objects), the role of neuromodulators, and known heterogeneity of the interneurons. These weaknesses make it difficult for readers to know the relevance of the simulations for experiments and for advancing theoretical understanding.

Strengths:

The authors use conductance-based Hodgkin-Huxley-like equations to simulate spiking activity in a network of neurons intended to model more accurately songbird nucleus HVC of adult male zebra finches. Spiking models are much closer to experiments than models based on firing rates or on 2-state neurons.

The authors include information deduced from modeling experimental current-clamp data such as the types and properties of conductances. They also take into account how neurons in one class connect to neurons in other classes via excitatory or inhibitory synapses, based on sparse paired recordings in slices by other researchers. The authors obtain some new results of modest interest such as how changes in the maximum conductances of four key channels (e.g., A-type K+ currents or Ca-dependent K+ currents) influence the structure and propagation of bursts, while simultaneously being able to mimic accurately current-clamp voltage measurements.

Weaknesses:

One weakness of this paper is the lack of a clearly stated, interesting, and relevant scientific question to try to answer. In the introduction, the authors do not discuss adequately which questions recent experimental and theoretical work have failed to explain adequately, concerning HVC neural dynamics and its role in producing vocalizations. The authors do not discuss adequately why they chose the approach of their paper and how their results address some of these questions.

For example, the authors need to explain in more detail how their calculations relate to the works of Daou et al, J. Neurophys. 2013 (which already fitted spiking models to neuronal data and identified certain conductances), to Jin et al J. Comput. Neurosci. 2007 (which already discussed how to get bursts using some experimental details), and to the rather similar paper by E. Armstrong and H. Abarbanel, J. Neurophys 2016, which already postulated and studied sequences of microcircuits in HVC. This last paper is not even cited by the authors.

We thank the reviewer for this valuable comment, and we agree that we did not clarify enough throughout the paper the utility of our model or how it advanced our understanding of the HVC dynamics and circuitry. To that end, we revised several places of the manuscript and made sure to cite and highlight the relevance and relatedness of the mentioned papers.

In short, and as mentioned to Reviewer 1, while several models of how sequence is generated within HVC have been proposed (Cannon et al., 2015; Drew & Abbott, 2003; Egger et al., 2020; Elmaleh et al., 2021; Galvis et al., 2018; Gibb et al., 2009a, 2009b; Hamaguchi et al., 2016; Jin, 2009; Long & Fee, 2008; Markowitz et al., 2015; Jin et al., 2007), all the models proposed either rely on intrinsic HVC circuitry to propagate sequential activity, rely on extrinsic feedback to advance the sequence or rely on both. These models do not capture the complex details of spike morphology, do not include the right ionic currents, do not incorporate all classes of HVC neurons, or do not generate realistic firing patterns as seen in vivo. Our model is the first biophysically realistic model that incorporates all classes of HVC neurons and their intrinsic properties. 

No existing hypothesis had been challenged with our model, rather; our model is a distillation of the various models that’s been proposed for the HVC network. We go over this in detail in the Discussion. We believe that the network model we developed provide a step forward in describing the biophysics of HVC circuitry, and may throw a new light on certain dynamics in the mammalian brain, particularly the motor cortex and the hippocampus regions where precisely-timed sequential activity is crucial. We suggest that temporally-precise sequential activity may be a manifestation of neural networks comprised of chain of microcircuits, each containing pools of excitatory and inhibitory neurons, with local interplay among neurons of the same microcircuit and global interplays across the various microcircuits, and with structured inhibition as well as intrinsic properties synchronizing the neuronal pools and stabilizing timing within a firing sequence.

The authors' main achievement is to show that simulations of a certain simplified and idealized network of spiking neurons, which includes some experimental details but ignores many others, match some experimental results like current-clamp-derived voltage time series for the three classes of HVC neurons (although this was already reported in earlier work by Daou and collaborators in 2013), and simultaneously the robust propagation of bursts with properties similar to those observed in experiments. The authors also present results about how certain neuronal details and burst propagation change when certain key maximum conductances are varied. However, these are weak conclusions for two reasons. First, the authors did not do enough calculations to allow the reader to understand how many parameters were needed to obtain these fits and whether simpler circuits, say with fewer parameters and simpler network topology, could do just as well. Second, many previous researchers have demonstrated robust burst propagation in a variety of feed-forward models. So what is new and important about the authors' results compared to the previous computational papers?

A major novelty of our work is the incorporation of experimental data with detailed network models. While earlier works have established robust burst propagation, our model uses realistic ion channel kinetics and feedback inhibition not only to reproduce experimental neural activity patterns but also to suggest prospective mechanisms for song sequence production in the most biophysical way possible. This aspect that distinguishes our work from other feed-forward models. We go over this in detail in the Discussion. However, the reviewer is right regarding the details of the calculations conducted for the fits, we will make sure to highlight this in the Methods and throughout the manuscript with more details.

We believe that the network model we developed provide a step forward in describing the biophysics of HVC circuitry, and may throw a new light on certain dynamics in the mammalian brain, particularly the motor cortex and the hippocampus regions where precisely-timed sequential activity is crucial. We suggest that temporally-precise sequential activity may be a manifestation of neural networks comprised of chain of microcircuits, each containing pools of excitatory and inhibitory neurons, with local interplay among neurons of the same microcircuit and global interplays across the various microcircuits, and with structured inhibition as well as intrinsic properties synchronizing the neuronal pools and stabilizing timing within a firing sequence.

Also missing is a discussion, or at least an acknowledgment, of the fact that not all of the fine experimental details of undershoots, latencies, spike structure, spike accommodation, etc may be relevant for understanding vocalization. While it is nice to know that some models can match these experimental details and produce realistic bursts, that does not mean that all of these details are relevant for the function of producing precise vocalizations. Scientific insights in biology often require exploring which of the many observed details can be ignored and especially identifying the few that are essential for answering some questions. As one example, if HVC-X neurons are completely removed from the authors' model, does one still get robust and reasonable burst propagation of HVC-RA neurons? While part of the nucleus HVC acts as a premotor circuit that drives the nucleus RA, part of HVC is also related to learning. It is not clear that HVC-X neurons, which carry out some unknown calculation and transmit information to area X in a learning pathway, are relevant for burst production and propagation of HVCRA neurons, and so relevant for vocalization. Simulations provide a convenient and direct way to explore questions of this kind.

One key question to answer is whether the bursting of HVC-RA projection neurons is based on a mechanism local to HVC or is some combination of external driving (say from auditory nuclei) and local circuitry. The authors do not contribute to answering this question because they ignore external driving and assume that the mechanism is some kind of intrinsic feed-forward circuit, which they put in by hand in a rather arbitrary and poorly justified way, by assuming the existence of small microcircuits consisting of a few HVC-RA, HVC-X, and HVC-I neurons that somehow correspond to "sub-syllabic segments". To my knowledge, experiments do not suggest the existence of such microcircuits nor does theory suggest the need for such microcircuits. 

Recent results showed a tight correlation between the intrinsic properties of neurons and features of song (Daou and Margoliash 2020, Medina and Margoliash 2024), where adult birds that exhibit similar songs tend to have similar intrinsic properties. While this is relevant, we acknowledge that not all details may be necessary for every aspect of vocalization, and future models could simplify concentrate on core dynamics and exclude certain features while still providing insights into the primary mechanisms.

The question of whether HVC_X neurons are relevant for burst propagation given that our model includes these neurons as part of the network for completeness, the reviewer is correct, the propagation of sequential activity in this model is primarily carried by HVC_RA neurons in a feed-forward manner, but only if there is no perturbation to the HVC network. For example, we have shown how altering the intrinsic properties of HVC_X neurons or for interneurons disrupts sequence propagation. In other words, while HVC neurons are the key forces to carry the chain forward, the interplay between excitation and inhibition in our network as well as the intrinsic parameters for all classes of HVC neurons are equally important forces in carrying the chain of activity forward. Thus, the stability of activity propagation necessary for song production depend on a finely balanced network of HVC neurons, with all classes contributing to the overall dynamics.

We agree with the reviewer however that a potential drawback of our model is that its sole focus is on local excitatory connectivity within the HVC (Kornfeld et al., 2017; Long et al., 2010), while HVC neurons receive afferent excitatory connections (Akutagawa & Konishi, 2010; Nottebohm et al., 1982) that plays significant roles in their local dynamics. For example, the excitatory inputs that HVC neurons receive from Uvaeformis may be crucial in initiating (Andalman et al., 2011; Danish et al., 2017; Galvis et al., 2018) or sustaining (Hamaguchi et al., 2016) the sequential activity. While we acknowledge this limitation, our main contribution in this work is the biophysical insights onto how the patterning activity in HVC is largely shaped by the intrinsic properties of the individual neurons as well as the synaptic properties where excitation and inhibition play a major role in enabling neurons to generate their characteristic bursts during singing. This is true and holds irrespective of whether an external drive is injected onto the microcircuits or not. We elaborated on this further in the revised version in the Discussion.

Another weakness of this paper is an unsatisfactory discussion of how the model was obtained, validated, and simulated. The authors should state as clearly as possible, in one location such as an appendix, what is the total number of independent parameters for the entire network and how parameter values were deduced from data or assigned by hand. With enough parameters and variables, many details can be fit arbitrarily accurately so researchers have to be careful to avoid overfitting. If parameter values were obtained by fitting to data, the authors should state clearly what the fitting algorithm was (some iterative nonlinear method, whose results can depend on the initial choice of parameters), what the error function used for fitting (sum of least squares?) was, and what data were used for the fitting.

The authors should also state clearly the dynamical state of the network, the vector of quantities that evolve over time. (What is the dimension of that vector, which is also the number of ordinary differential equations that have to be integrated?) The authors do not mention what initial state was used to start the numerical integrations, whether transient dynamics were observed and what were their properties, or how the results depended on the choice of the initial state. The authors do not discuss how they determined that their model was programmed correctly (it is difficult to avoid typing errors when writing several pages or more of a code in any language) or how they determined the accuracy of the numerical integration method beyond fitting to experimental data, say by varying the time step size over some range or by comparing two different integration algorithms.

We thank the reviewer again. The fitting process in our model occurred only at the first stage where the synaptic parameters were fit to the Mooney and Prather as well as the Kosche results. There was no data shared and we merely looked at the figures in those papers and checked the amplitude of the elicited currents, the magnitudes of DC-evoked excitations etc … and we replicated that in our model. While this is suboptimal, it was better for us to start with it rather than simply using equations for synaptic currents from the literature for other types of neurons (that are not even HVC’s or in the songbird) and integrate them into our network model. The number of ODEs that govern the dynamics of every model neuron is listed on page 10 of the manuscript as well as in the Appendix.  Moreover, we highlighted the details of this fitting process in the revised version.

Also disappointing is that the authors do not make any predictions to test, except rather weak ones such as that varying a maximum conductance sufficiently (which might be possible by using dynamic clamps) might cause burst propagation to stop or change its properties. Based on their results, the authors do not make suggestions for further experiments or calculations, but they should.

We agree that making experimental testable predictions is crucial for the advancement of the model. Our predictions include testing whether eradication of a class of neurons such as HVC_X neurons disrupts activity propagation which can be done through targeted neuron elimination. This also can be done through preventing rebound bursting in HVC_X by pharmacologically blocking the I_H channels. Others include down regulation of certain ion channels (pharmacologically done through ion blockers) and testing which current is fundamental for song production (and there a plenty of test based our results, like the SK current, the T-type Ca²⁺ current, the A-type K⁺ current, etc…). We incorporated these into the Discussion of the revised manuscript to better demonstrate the model's applicability and to guide future research directions.

Main issues:

(1) Parameters are overly fine-tuned and often do not match known biology to generate chains. This fine-tuning does not reveal fundamental insights.

(1a) Specific conductances (e.g. AMPA) are finely tweaked to generate bursts, in part due to a lack of a dendritic mechanism for burst generation. A dendritic mechanism likely reflects the true biology of HVC neurons.

We acknowledge that the model does not include active dendritic processes and we do not regard this as a limitation. In fact, our present approach, although simplified, is intended to focus on somatic mechanisms to identify minimal conditions required for stable sequential propagation. We know HVC_RA neurons possess thin, spiny dendrites which can contribute to burst initiation and shaping. Future models that include such nonlinear dendritic mechanisms would likely reduce the need for fine tuning of specific conductances at the soma and consequently better match the known biology of HVC_RA neurons. 

In text: “While our simplified, somatically driven architecture enables better exploration of mechanisms for sequence propagation, future extensions of the model will incorporate dendritic compartments to more accurately reflect the intrinsic bursting mechanisms observed in HVC_RA neurons.”

(1b) In this paper, microcircuits are simulated and then concatenated to make the HVC chain, resulting in no representations during silent gaps. This is out of touch with the known HVC function. There is no anatomical nor functional evidence for microcircuits of the kind discussed in this paper or in the earlier and rather similar paper by Eve Armstrong and Henry Abarbanel (J. Neurophy 2016). One can write a large number of papers in which one makes arbitrary unconstrained guesses of network structure in HVC and, unless they reveal some novel principle or surprising detail, they are all going to be weak.

Although the model is composed of sequentially activated microcircuits, the gaps between each microcircuit’s output do not represent complete silence in the network. During these periods, other neurons such as those in other microcircuits may still exhibit bursting activity. Thus, what may appear as a 'silent gap' from the perspective of a given output microcircuit is, in fact, part of the ongoing background dynamics of the larger HVC neuron network. We fully acknowledge the reviewer's point that there is no direct anatomical or physiological evidence supporting the presence of microcircuits with this structure in HVC. Our intention was not to propose the existence of such a physical model but to use it as a computational simplification to make precise sequential bursting activity feasible given the biologically realistic neuronal dynamics used. Hence, our use of 'microcircuits' refers to a modeling construct rather than a structural hypothesis. Even if the network topology is hypothetical, we still believe that the temporal structuring suggested allows us to generate specific predictions for future work about burst timing and neuronal connections.

(1c) HVC interneuron discharge in the author's model is overly precise; addressing the observation that these neurons can exhibit noisy discharge. Real HVC interneurons are noisy. This issue is critical: All reviewers strongly recommend that the authors should, at the minimum in a revision, focus on incorporating HVC-I noise in their model.

We agree that capturing the variability in interneuron bursting is critical for biological realism. In our model, HVC interneurons receive stochastic background current that introduces variability in their firing patterns as observed in vivo. This variability is seen in our simulations and produces more biologically realistic dynamics while maintaining sequence propagation. We clarify this implementation in the Methods section. 

(1d) Address the finding that Kosche et al show that even with reduced inhibition, HVCra neuronal timing is preserved; it is the burst pattern that is affected.

The differences between the Kosche et al. (2015) findings and the predictions of our model arise from differences in the aspect of HVC function we are modeling. Our model is more sensitive to inhibition, which is a designed mechanism for achieving precise song patterning. This is a modeling simplification we adopted to capture specific characteristics of HVC function. 

We acknowledged this point in the discussion: “While findings of Kosche et al. (2015) emphasize the robustness of the HVC timing circuit to inhibition, our model is more sensitive to inhibition, highlighting that HVC likely operates with several, redundant mechanisms that overall ensure temporal precision.”

(1e) The real HVC is robust to microlesions, cooling, and HVCra neuron turnover. The model in this paper relies on precise HVCra connectivity and is not robust.

Although our model is grounded in the biologically observed behavior of HVC neurons in vivo, we don’t claim that it fully captures the resilience seen in the HVC network. Instead, we see this as a simplified framework that helps us explore the basic principles of sequential activity. In the future, adding features like recurrent excitation, synaptic plasticity, or homeostatic mechanisms could make the model more robust.

(1f) There is unclear motivation for Ih-driven HVCx bursting, given past findings from the Mooney group.

Daou et al (2013) noticed that the observed in HVC_X and HVC_INT neurons in response to hyperpolarizing current pulses (Dutar et al. 1998; Kubota and Saito 1991; Kubota and Taniguchi 1998) was completely abolished after the application of the drug ZD 7288 in all of the neurons tested indicating that the sag in these HVC neurons is due to the hyperpolarization-activated inward current (I_h). in addition, the sag and the rebound seen in these two neuron groups were larger as for larger hyperpolarization current pulses.

(1g) The initial conditions of the network and its activity under those conditions, as well as the possible reliance on external inputs, are not defined.

In our model, network activity is initiated through a brief, stochastic excitatory input to a small HVC_RA neuron of one microcircuit. This drive represents a simplified version of external input from upstream brain regions known to project to HVC, such as nuclei in the high vocal center's auditory pathways such as Nif and Uva. Modeling the activity of these upstream regions and their influence on HVC dynamics is an ongoing research work to be published in the future.

(1h) It has been known from the time of Hodgkin and Huxley how to include temperature dependences for neuronal dynamics so another suggestion is for the authors to add such dependences for the three classes of neurons and see if their simulation causes burst frequencies to speed up or slow down as T is varied.

We added this as limitation to the discussion section: “Our model was run at a fixed physiological temperature, but it's well known going all the way back to Hodgkin and Huxley that both ion channel activity and synaptic dynamics can change with temperature. In future work, adding temperature scaling (like Q10 factors) could help us explore how burst timing and sequence speed change with temperature changes, and how neural activity in HVC would/would not preserve its precision under different physiological conditions.”

(2) The scope of the paper and its objectives must be clearly defined. Defining the scope and providing caveats for what is not considered will help the reader contextualize this study with other work.

(2a) The paper does not consider the role of external inputs to HVC, which are very likely important for the capacity of the HVC chain to tile the entire song, including silent gaps.

The role of afferent input to HVC particularly from nuclei such as Uva and Nif is critical in shaping the timing and initiation of HVC sequences throughout the song, including silent intervals. In fact, external inputs are likely involved in more than just triggering sequences, they may also influence the continuity of activity across motifs. However, in this study, we chose to focus on the intrinsic dynamics of HVC as a step toward understanding the internal mechanisms required for generating temporally precise sequences and for this reason, we used a simplified external input only to initiate activity in the chain.

(2b) The paper does not consider important dendritic mechanisms that almost certainly facilitate the all-or-none bursting behavior of HVC projection neurons. the authors need to mention and discuss that current-clamped neuronal response - in which an electrode is inserted into the soma and then a constant current-step is applied - bypasses dendritic structure and dendritic processing and so is an incomplete way to characterize a neuron's properties. In particular, claiming to fit current-clamp data accurately and then claiming that one now has a biophysically accurate network model, as the authors do, is greatly misleading.

While we addressed this is 1a, we do not suggest that our model is a fully accurate biophysical representation of HVC network. Instead, we see it as a simplified framework that helps reveal how much of HVC’s sequential activity can be explained by somatic properties and synaptic interactions alone. However, additional biological mechanisms, like dendritic processing, are likely to play an important role and should be explored in future work.

(2c) The introduction does not provide a clear motivation for the paper - what hypotheses are being tested? What is at stake in the model outcomes? It is not inherently informative to take a known biological representation and fine-tune a limited model to replicate that representation.

We explicitly added the hypotheses to the revised introduction.

(2d) There have been several published modeling efforts applied to the HVC chain (Seung, Fee, Long, Greenside, Jin, Margoliash, Abarbanel). These and others need to be introduced adequately, and it needs to be crystal clear what, if anything, the present study is adding to the canon.

While several influential models have explored how HVC might generate sequences ranging from synfire chains to recurrent dynamics or externally driven sequences (e.g., Seung, Fee, Long, Greenside, Jin, Abarbanel, and others), these models could not capture the detailed dynamics observed in vivo. Our aim was to bridge a gap in the modeling literature by exploring how far biophysically grounded intrinsic properties and experimentally supported synaptic connections that are local to the HVC can alone produce temporally precise sequences. We have proven that these mechanisms are sufficient to generate these sequences, although some missing components (such as dendritic mechanisms or external inputs) might be needed to fully capture the complexity and robustness of HVC function.

(2e) The authors mention learning prominently in the abstract, summary, and introduction but this paper has nothing to do with learning. Most or all mentions of learning should be deleted since they are misleading.

We appreciate the reviewer’s observation however our intent by referencing learning was not to suggest that our model directly simulates learning processes, but rather to place HVC function within the broader context of song learning and production, where temporal sequencing plays a fundamental role. Yet, repeated references to learning may be misleading given that our current model does not incorporate plasticity, synaptic modification, or developmental changes. Hence, we have carefully revised the manuscript to rephrase mentions of learning unless directly relevant to context. 

(3) Using the model for hypothesis generation and prediction of experimental results.

(3a) The utility of a model is to provide conceptual insight into how or why the real HVC functions as it does, or to predict outcomes in yet-to-be conducted experiments to help motivate future studies. This paper does not adequately achieve these goals.

We revised the Discussion of the manuscript to better emphasize potential contributions and point out many experiments that could validate or challenge the model’s predictions. These include dynamic clamp or ion channel blockers targeting A-type K⁺ in HVC_RA neurons to assess their impact on burst precision, optogenetic disruption of inhibitory interneurons to observe changes in burst timing and sequence propagation, pharmacological modulation of I_h or I_CaT in HVC_X and interneurons etc. 

(3b) Additionally, it can be interesting to conduct an experiment on an existing model; for example, what happens to the HVCra chain in your model if you delete the HVCx neurons? What happens if you block NMDA receptors? Such an approach in a modeling paper can help motivate hypotheses and endow the paper with a sense of purpose.

We agree that running targeted experiments to test our computational model such as removing an HVC neuron population or blocking a synaptic receptor can be a powerful way to generate new ideas and guide future experiments. While we didn’t include these specific tests in the current study, the model is well suited for this kind of exploration. For instance, removing interneurons could help us better understand their role in shaping the timing of HVC_RA bursts. These are great directions for future experiments, and we now highlight this in the discussion as a way the model could be used to guide experiments.

(4) Changes to the paper's organization may improve clarity.

(4a) Nearly all equations should be moved to an Appendix so that the main part of the paper can focus on the science: assumptions made, details of simulations, conclusions obtained, and their significance. The authors present many equations without discussion which weakens the paper.

Equations moved to appendix.

(4b) There are many grammatical errors, e.g., verbs do not match the subject in terms of being single or plural. The authors need to run their manuscript through a grammar checker.

Done.

(4c) Many of the figures are poorly designed and should be substantially modified. E.g. in Figure 1B, too many colors are used, making it hard to grasp what is being plotted and the colors are not needed. Figures 1C and 1D are entire figures taken from other papers, and there is no way a reader will be able to see or appreciate all the details when this figure is published on a single page. Figure 2 uses colors for dots that are almost identical, and the colors could be avoided by using different symbols. Figure 5 fills an entire page but most of the figure conveys no information, there is no need to show the same details for all 120 neurons, just show the top 1/3 of this figure; the same for Figure 7, a lot of unnecessary information is being included. Figure 10, the bottom time series of spikes should be replaced with a time series of rates, cannot extract useful information.

Adjusted as requested. 

(4d) Table 1 is long and largely uninteresting, and should be moved to an appendix.

Table 1 moved to appendix.

(4e) Many sentences are not carefully written, which greatly weakens the paper. As one typical example, the first sentence in the Discussion section "In this study, we have designed a neural network model that describes [sic] zebra finch song production in the HVC." This is inaccurate, the model does not describe song production, it just explores some properties of one nucleus involved with song production. Just one or few sentences like this is ok but there are so many sentences of this kind that the reader loses faith in the authors.

Thank you for raising this point, we revised the manuscript to improve the precision of the writing. We replaced the first sentence of the discussion with this: "In this study, we developed a biophysically realistic neural network model to explore how intrinsic neuronal properties and local connectivity within the songbird nucleus HVC may support the generation of temporally precise activity sequences associated with zebra finch song."

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary

The authors previously published a study of RGC boutons in the dLGN in developing wild-type mice and developing mutant mice with disrupted spontaneous activity. In the current manuscript, they have broken down their analysis of RGC boutons according to the number of Homer/Bassoon puncta associated with each vGlut3 cluster.

The authors find that, in the first post-natal week, RGC boutons with multiple active zones (mAZs) are about a third as common as boutons with a single active zone (sAZ). The size of the vGluT2 cluster associated with each bouton was proportional to the number of active zones present in each bouton. Within the author's ability to estimate these values (n=3 per group, 95% of results expected to be within ~2.5 standard deviations), these results are consistent across groups: 1) dominant eye vs. nondominant eye, 2) wild-type mice vs. mice with activity blocked, and at 3) ages P2, P4, and P8. The authors also found that mAZs and sAZs also have roughly the same number (about 1.5) of sAZs clustered around them (within 1.5 um).

However, the authors do not interpret this consistency between groups as evidence that active zone clustering is not a specific marker or driver of activity dependent synaptic segregation. Rather, the authors perform a large number of tests for statistical significance and cite the presence or absence of statistical significance as evidence that "Eye-specific active zone clustering underlies synaptic competition in the developing visual system (title)". I don't believe this conclusion is supported by the evidence.

We have revised the title to be descriptive: "Eye-specific differences in active zone addition during synaptic competition in the developing visual system." While our correlative approach does not establish direct causality, our findings provide important structural evidence that complements existing functional studies of activity-dependent synaptic refinement. We have carefully revised the text throughout to avoid causal language, focusing instead on the developmental patterns we observe.

Strengths

The source dataset is high resolution data showing the colocalization of multiple synaptic proteins across development. Added to this data is labeling that distinguishes axons from the right eye from axons from the left eye. The first order analysis of this data showing changes in synapse density and in the occurrence of multi-active zone synapses is useful information about the development of an important model for activity dependent synaptic remodeling.

Weaknesses

In my previous review I argued that it was not possible to determine, from their analysis, whether the differences they were reporting between groups was important to the biology of the system. The authors have made some changes to their statistics (paired t-tests) and use some less derived measures of clustering. However, they still fail to present a meaningfully quantitative argument that the observed group differences are important. The authors base most of their claims on small differences between groups. There are two big problems with this practice. First, the differences between groups appear too small to be biologically important. Second, the differences between groups that are used as evidence for how the biology works are generally smaller than the precision of the author's sampling. That is, the differences are as likely to be false positives as true positives.

(1) Effect size. The title claims: "Eye-specific active zone clustering underlies synaptic competition in the developing visual system". Such a claim might be supported if the authors found that mAZs are only found in dominant-eye RGCs and that eye-specific segregation doesn't begin until some threshold of mAZ frequency is reached. Instead, the behavior of mAZs is roughly the same across all conditions. For example, the clear trend in Figure 4C and D is that measures of clustering between mAZ and sAZ are as similar as could reasonably be expected by the experimental design. However, some of the comparisons of very similar values produced p-values < 0.05. The authors use this fact to argue that the negligible differences between mAZ and sAZs explain the development of the dramatic differences in the distribution of ipsilateral and contralateral RGCs.

We have changed the title to avoid implying a causal relationship between clustering and eye-specific segregation. Our key findings in Figures 4C and 4D demonstrate effect sizes >2.0 with high statistical power (Supplemental Table S2). While the absolute magnitude of differences is modest (5-7%), these high effect sizes combined with low inter-animal variability demonstrate consistent, reproducible biological phenomena. During development, small differences during critical periods can have profound downstream consequences for synaptic refinement outcomes.

We acknowledge that significance in Figure 4 arises due to low variance between biological replicates rather than large mean differences. We have revised the text to describe these as "slight" differences and that "WT mice show a tendency toward forming more synapses near mAZ inputs," reflecting appropriate caution in our interpretation while maintaining the statistical robustness of our findings.

(2) Sample size. Performing a large number of significance tests and comparing pvalues is not hypothesis testing and is not descriptive science. At best, with large sample sizes and controls for multiple tests, this approach could be considered exploratory. With n=3 for each group, many comparisons of many derived measures, among many groups, and no control for multiple testing, this approach constitutes a random result generator.

The authors argue that n=3 is a large sample size for the type of high resolution / large volume data being used. It is true that many electron microscopy studies with n=1 are used to reveal the patterns of organization that are possible within an individual. However, such studies cannot control individual variation and are, therefore, not appropriate for identifying subtle differences between groups.

In response to previous critiques along these lines, the authors argue they have dealt with this issue by limiting their analysis to within-individual paired comparisons. There are several problems with their thinking in this approach. The main problem is that they did not change the logic of their arguments, only which direction they pointed the t-tests. Instead of claiming that two groups are different because p < 0.05, they say that two groups are different because one produced p < 0.05 and the other produced p > 0.05. These arguments are not statistically valid or biologically meaningful.

We have implemented rigorous statistical controls, applying false discovery rate (FDR) correction using the Benjamini-Hochberg method (α = 0.05) within each experimental condition (age × genotype combination). This correction strategy treats each condition as addressing a distinct experimental question: “What synaptic properties differ between left eye and right eye inputs in this specific developmental stage and genotype?” The approach appropriately controls for multiple testing while preserving power to detect biologically meaningful differences. We applied FDR correction separately to the ~20-34 measurements (varying by age and genotype) within each of the six experimental conditions, resulting in condition-specific adjusted p-values reported in updated Supplemental Table S2. This correction confirmed the robustness of our key findings. We do not base conclusions solely on comparing p-values across conditions. Our interpretations focus on effect sizes, confidence intervals, and consistent patterns within each condition, with statistical significance providing supporting evidence rather than the primary basis for biological conclusions.

To the best of my understanding, the results are consistent with the following model:

RGCs form mAZs at large boutons (known)

About a quarter of week-one RGC boutons are mAZs (new observation)

Vesicle clustering is proportional to active zone number (~new observation)

RGC synapse density increases during the first post-week (known)

Blocking activity reduces synapse density (known)

Contralateral eye RGCs for more and larger synapses in the lateral dLGN (known)

While mAZ formation is known in adult and juvenile dLGN, the formation of mAZ boutons during eye-specific competition represents new information with important functional implications. Synapses with multiple release sites should be stronger than single-active-zone synapses, suggesting a structural correlate for competitive advantage during refinement.

We demonstrate distinct developmental patterns for sAZ versus mAZ contacts during the first postnatal week. Multi-active zone density favors the dominant eye, while single active-zone synapse density from the competing eye increases from P2-P4 to match dominant-eye levels. This reveals that newly formed synapses from the competing eye predominantly contain single release sites, marking P4-P8 as a critical window for understanding molecular mechanisms driving synaptic elimination.

Our results show that altered retinal activity patterns (β2KO mice) reduce synapse density during eye-specific competition. We relied on β2 knockout mice, which retain retinal waves and spontaneous spike activity but with disrupted patterns and output levels compared to controls. We make no claims about complete activity blockade. Previous studies using different activity manipulations (epibatidine, TTX) have examined terminal morphology, but effects on synapse density during competition remain largely unknown. Achieving complete retinal activity blockade is technically challenging, making it of interest to revisit the role of activity using more precise manipulations to control spike output and relative timing.

With n=3 and effect sizes smaller than 1 standard deviation, a statistically significant result is about as likely to be a false positive as a true positive.

A true-positive statistically significant result does is not evidence of a meaningful deviation from a biological model.

Our conclusions are based on results with effect sizes substantially larger than 1. Key findings demonstrate effect sizes exceeding 2.0. These large effect sizes, combined with rigorous FDR correction and low inter-animal variability, provide evidence against false positive results. During critical developmental periods, consistent structural differences, even those modest in absolute magnitude, can reflect important regulatory mechanisms that influence refinement outcomes. All statistical results, effect sizes, and power analyses are reported in Supplementary Tables S2, with confidence intervals in Supplementary Table S3. We have revised the text in several places where small differences are presented to reflect appropriate caution in our interpretation.

Providing plots that show the number of active zones present in boutons across these various conditions is useful. However, I could find no compelling deviation from the above default predictions that would influence how I see the role of mAZs in activity dependent eye-specific segregation.

Below are critiques of most of the claims of the manuscript.

Claim (abstract): individual retinogeniculate boutons begin forming multiple nearby presynaptic active zones during the first postnatal week.

Confirmed by data.

Claim (abstract): the dominant-eye forms more numerous mAZ contacts,

Misleading: The dominant-eye (by definition) forms more contacts than the nondominant eye. That includes mAZ.

While the dominant eye forms more total contacts, the pattern depends critically on contact type and developmental stage. The dominant eye forms more mAZ contacts across all ages (Figures 2 and S1). However, for sAZ contacts, the two eyes form similar numbers at P4, with the non-dominant eye showing increased sAZ formation during this critical period. This differential pattern by synapse type represents an important aspect of how synaptic competition unfolds structurally.

Claim (abstract): At the height of competition, the non-dominant-eye projection adds many single active zone (sAZ) synapses

Weak: While the individual observation is strong, it is a surprising deviation based on a single n=3 experiment in a study that performed twelve such experiments (six ages, mutant/wildtype, sAZ/mAZ)

The difference in eye-specific sAZ formation at P2 and P8 had effect sizes of ~5.3 and ~2.7 respectively (after FDR correction the difference was still significant at P2 and trending at P8). At P4, no effect was observed by paired T-test and the 5/95% confidence intervals ranged from -0.021-0.008 synapses/m³. The consistency of this pattern across P2 and P8, combined with the large effect sizes, supports the reliability of this developmental finding. We report all effect sizes and power test analyses in Supplemental Table S2, and confidence intervals in Supplemental Table S3. 

Claim (abstract): Together, these findings reveal eye-specific differences in release site addition during synaptic competition in circuits essential for visual perception and behavior.

False: This claim is unambiguously false. The above findings, even if true, do not argue for any functional significance to active zone clustering.

Our phrasing “circuits essential for visual perception and behavior” referred to the general importance of binocular organization in the retinogeniculate system for visual processing and we did not intend to claim direct functional significance of our structural data. For clarity we have deleted the latter part of this sentence. In lines 35-37, the abstract now reads “Together, these findings reveal eye-specific differences in release site addition that correlate with axonal refinement outcomes during retinogeniculate refinement.”

Claim (line 84): "At the peak of synaptic competition midway through the first postnatal week, the non-dominant-eye formed numerous sAZ inputs, equalizing the global synapse density between the two eyes"

Weak: At one of twelve measures (age, bouton type, genotype) performed with 3 mice each, one density measure was about twice as high as expected.

The difference in eye-specific sAZ formation at P2 and P8 had effect sizes of ~5.3 and ~2.7 respectively (after FDR correction the difference was still significant at P2 and trending at P8). At P4, no effect was observed by paired T-test and the 5/95% confidence intervals ranged from -0.021-0.008 synapses/m³. The consistency of this pattern across P2 and P8, combined with the large effect sizes, supports the reliability of this developmental finding. We report all effect sizes and power test analyses in Supplemental Table S2, and confidence intervals in Supplemental Table S3. 

Claim (line 172): "In WT mice, both mAZ (Fig. 3A, left) and sAZ (Fig. 3B, left) inputs showed significant eye-specific volume differences at each age."

Questionable: There appears to be a trend, but the size and consistency is unclear.

Claim (line 175): "the median VGluT2 cluster volume in dominant-eye mAZ inputs was 3.72 fold larger than that of non-dominant-eye inputs (Fig. 3A, left)."

Cherry picking. Twelve differences were measured with an n of 3, 3 each time. The biggest difference of the group was cited. No analysis is provided for the range of uncertainty about this measure (2.5 standard deviations) as an individual sample or as one of twelve comparisons.

Claim (line 174): "In the middle of eye-specific competition at P4 in WT mice, the median VGluT2 cluster volume in dominant-eye mAZ inputs was 3.72 fold larger than that of non-dominant-eye inputs (Fig. 3A, left). In contrast, β2KO mice showed a smaller 1.1 fold difference at the same age (Fig. 3A, right panel). For sAZ synapses at P4, the magnitudes of eye-specific differences in VGluT2 volume were smaller: 1.35-fold in WT (Fig. 3B, left) and 0.41-fold in β2KO mice (Fig. 3B, right). Thus, both mAZ and sAZ input size favors the dominant eye, with larger eye-specific differences seen in WT mice (see Table S3)."

No way to judge the reliability of the analysis and trivial conclusion: To analyze effect size the authors choose the median value of three measures (whatever the middle value is). They then make four comparisons at the time point where they observed the biggest difference in favor of their hypothesis. There is no way to determine how much we should trust these numbers besides spending time with the mislabeled scatter plots. The authors then claim that this analysis provides evidence that there is a difference in vGluT2 cluster volume between dominant and non-dominant RGCs and that that difference is activity dependent. The conclusion that dominant axons have bigger boutons and that mutants that lack the property that would drive segregation would show less of a difference is very consistent with the literature. Moreover, there is no context provided about what 1.35 or 1.1 fold difference means for the biology of the system.

We focused on P4 for biological reasons rather than post-hoc selection. P4 represents the established peak of synaptic competition when eye-specific synapse densities are globally equivalent. This is a timepoint consistently highlighted throughout our manuscript and supported by previous literature. We have modified our presentation from fold changes to measured eye-specific differences in volume (mean ± standard error) and added confidence intervals in Supplemental Table S3. The effect sizes for eye-specific differences in VGluT2 volume at P4 are robust: ~2.3 and ~1.5 for mAZ and sAZ measurements in WT mice, and ~2.5 and ~1.8 in β2KO mice, with all analyses well-powered (Supplemental Table S2).

We were unable to identify any mislabeled scatter plots and believe all figures are correctly labeled. While dominant-eye advantage in bouton size is consistent with previous literature, our study provides the first detailed analysis of how this develops specifically during the critical period of competition, with distinct patterns for single versus multi-active zone contacts. Our data show that dominant-eye inputs have larger vesicle pools that scale with active zone number. While this suggests enhanced transmission capacity, we make no direct physiological claims based on structural data alone.

Claim (189): "This shows that vesicle docking at release sites favors the dominant-eye as we previously reported but is similar for like eye type inputs regardless of AZ number."

Contradicts core claim of manuscript: Consistent with previous literature, there is an activity dependent relative increase in vGlut2 clustering of dominant eye RGCs. The new information is that that activity dependence is more or less the same in sAZ and mAZ. The only plausible alternative is that vGlut2 scaling only increases in mAZ which would be consistent with the claims of their paper. That is not what they found. To the extent that the analysis presented in this manuscript tests a hypothesis, this is it. The claim of the title has been refuted by figure 3.

We report the volume of docked vesicle signal (VGluT2) nearby each active zone, finding this is greater for dominant-eye synapses. Within each eye-specific synapse population, vesicle signal per active zone is similar regardless of whether these are part of single- or multi-active zone contacts. This is consistent with a modular program of active zone assembly and maintenance: core molecular programs facilitate docking at each AZ similarly regardless of how many AZs are nearby. 

This finding does not contradict our main conclusions but rather provides insight into how synaptic advantages are structured. The dominant eye's advantage may arise in part from forming more multi-AZ contacts (which have proportionally more docked vesicles) rather than from enhanced vesicle loading per individual active zone. This organization may reflect how developmental competition operates through contact number and active zone addition rather than fundamental changes to individual release site properties.

We have changed the title to be descriptive rather than mechanistic.

Claim (line 235): "For the non-dominant eye projection, however, clustered mAZ inputs outnumbered clustered sAZ inputs at P4 (Fig. 4C, bottom left panel), the age when this eye adds sAZ synapses (Fig. 2C)."

Misleading: The overwhelming trend across 24 comparisons is that the sAZ clustering looks like mAZ clustering. That is the objective and unambiguous result. Among these 24 underpowered tests (n=3), there were a few p-values < 0.05. The authors base their interpretation of cell behavior on these crossings.

In Figures 4C and 4D we report significant results with high effect sizes (effect sizes all greater than 2; see Supplemental Table S2). The mean differences are modest (5-7%) and significance arises due to low variance between biological replicates. We acknowledge that clustering patterns are generally similar between mAZ and sAZ inputs across most conditions. We have revised the text to describe these as “slight” differences and that “WT mice show a tendency toward forming more synapses near mAZ inputs”, reflecting appropriate caution in our interpretation while noting the statistical consistency of these patterns.

Claim (line 328): "The failure to add synapses reduced synaptic clustering and more inputs formed in isolation in the mutants compared to controls."

Trivially true: Density was lower in mutant.

We have rewritten the sentence for clarity: “The failure to add synapses could explain the observation that synaptic clustering was reduced and more inputs formed in isolation in the mutants compared to controls.”

Claim (line 332): "While our findings support a role for spontaneous retinal activity in presynaptic release site addition and clustering..."

Not meaningfully supported by evidence: I could not find meaningful differences between WT and mutant beside the already known dramatic difference in synapse density.

We have changed the sentence to avoid overinterpreting the results. The new sentence in lines 415-417 reads: “While our results highlight developmental changes in presynaptic release site addition and clustering, activity-dependent postsynaptic mechanisms also influence input refinement at later stages.”

Reviewer #2 (Public review):

Summary:

In this manuscript, Zhang and Speer examine changes in the spatial organization of synaptic proteins during eye specific segregation, a developmental period when axons from the two eyes initially mingle and gradually segregate into eye-specific regions of the dorsal lateral geniculate. The authors use STORM microscopy and immunostain presynaptic (VGluT2, Bassoon) and postsynaptic (Homer) proteins to identify synaptic release sites. Activity-dependent changes of this spatial organization are identified by comparing the β2KO mice to WT mice. They describe two types of synapses based on Bassoon clustering: the multiple active zone (mAZ) synapse and single active zone (sAZ) synapse. In this revision, the authors have added EM data to support the idea that mAZ synapses represent boutons with multiple release sites. They have also reanalyzed their data set with different statistical approaches.

Strengths:

The data presented is of good quality and provides an unprecedented view at high resolution of the presynaptic components of the retinogeniculate synapse during active developmental remodeling. This approach offers an advance to the previous mouse EM studies of this synapse because of the CTB label allows identification of the eye from which the presynaptic terminal arises.

Weaknesses:

While the interpretation of this data set is much more grounded in this second revised submission, some of the authors' conclusions/statements still lack convincing supporting evidence. In particular, the data does not support the title: "Eye-specific active zone clustering underlies synaptic competition in the developing visual system". The data show that there are fewer synapses made for both contra- and ipsi- inputs in the β2KO mice-- this fact alone can account for the differences in clustering. There is no evidence linking clustering to synaptic competition. Moreover, the findings of differences in AZ# or distance between AZs that the authors report are quite small and it is not clear whether they are functionally meaningful.

We thank the reviewer for their helpful suggestions that improved the manuscript in this revision. We have changed the title to remove the reference to “clustering” and to avoid implying any causal relationships. The new title is descriptive: “Eye-specific differences in active zone addition during synaptic competition in the developing visual system”.

To further address the reviewers comments, we have removed the remaining references to activity-dependent effects on synaptic development (line 36, line 96, line 415). We have also modified the text in lines 411-413 to state that “The failure to add synapses could explain the observation that synaptic clustering was reduced and more inputs formed in isolation in the mutants compared to controls.”

We have also updated our presentation of results for Figure 4 to ensure that we do not causally link clustering to synaptic competition. In Figures 4C and 4D we report significant results with high effect sizes (effect sizes all greater than 2; see Supplemental Table S2). The mean differences are modest (5-7%) and significance arises due to low variance between biological replicates. We acknowledge that clustering patterns are generally similar between mAZ and sAZ inputs across most conditions. We have revised the text to describe these as “slight” differences and that “WT mice show a tendency toward forming more synapses near mAZ inputs”, reflecting appropriate caution in our interpretation while noting the statistical consistency of these patterns.

Reviewer #3 (Public review):

This study is a follow-up to a recent study of synaptic development based on a powerful data set that combines anterograde labeling, immunofluorescence labeling of synaptic proteins, and STORM imaging (Cell Reports, 2023). Specifically, they use anti-Vglut2 label to determine the size of the presynaptic structure (which they describe as the vesicle pool size), anti-Bassoon to label active zones with the resolution to count them, and anti-Homer to identify postsynaptic densities. Their previous study compared the detailed synaptic structure across the development of synapses made with contraprojecting vs. ipsi-projecting RGCs and compared this developmental profile with a mouse model with reduced retinal waves. In this study, they produce a new detailed analysis on the same data set in which they classify synapses into "multi-active zone" vs. "single-active zone" synapses and assess the number and spacing of these synapses. The authors use measurements to make conclusions about the role of retinal waves in the generation of same-eye synaptic clusters. The authors interpret these results as providing insight into how neural activity drives synapse maturation, the strength of their conclusions is not directly tested by their analysis.

Strengths:

This is a fantastic data set for describing the structural details of synapse development in a part of the brain undergoing activity-dependent synaptic rearrangements. The fact that they can differentiate the eye of origin is what makes this data set unique over previous structural work. The addition of example images from the EM dataset provides confidence in their categorization scheme.

Weaknesses:

Though the descriptions of single vs multi-active zone synapses are important and represent a significant advance, the authors continue to make unsupported conclusions regarding the biological processes driving these changes. Although this revision includes additional information about the populations tested and the tests conducted, the authors do not address the issue raised by previous reviews. Specifically, they provide no assessment of what effect size represents a biologically meaningful result. For example, a more appropriate title is "The distribution of eye-specific single vs multiactive zone is altered in mice with reduced spontaneous activity" rather than concluding that this difference in clustering is somehow related to synaptic competition. Of course, the authors are free to speculate, but many of the conclusions of the paper are not supported by their results.

We appreciate the reviewer’s helpful critique. We have changed the title to be descriptive and avoid implying causal relationships. 

We have applied false discovery rate (FDR) correction using the Benjamini-Hochberg method with α = 0.05 within each experimental condition (age × genotype combination). The FDR correction treats each condition as addressing a distinct experimental question: 'What synaptic properties differ between left eye and right eye inputs in this specific developmental stage and genotype?'

This correction strategy is appropriate because: 1) we focus our statistical comparisons within each age/genotype; 2) each age-genotype combination represents a separate biological context where different synaptic properties between eye-of-origin may be relevant; and 3) this approach controls for multiple testing within each experimental question while maintaining statistical power to detect meaningful biological differences.

We applied FDR correction separately to the ~20-34 measurements (varying with age and genotype) within each of the six experimental conditions (P2-WT, P2-ß2, P4-WT, P4-ß2, P8-WT, P8-ß2), resulting in condition-specific adjusted p-values. These are reported in the updated Supplemental Table S2. Figures have been also been updated to reflect the FDR-adjusted values. Selected between-genotype comparisons are presented descriptively using 5/95% confidence intervals. This correction confirmed the robustness of our key findings.

With regard to the biological significance of effect sizes, our key findings demonstrate effect sizes >2.0, indicating robust effects. During critical developmental periods, consistent structural differences, even those modest in absolute magnitude, can reflect important regulatory mechanisms that influence refinement outcomes. The differences in synaptic organization we observe occur during the first postnatal week when eyespecific competition is active, suggesting these patterns may be relevant to understanding how structural advantages emerge during synaptic refinement.

Reviewer #1 (Recommendations for the authors):

I have tried to understand the analysis and biology of this manuscript as best I can. I believe the analytical approach taken is not reliable and I have explained why in my public comments. I don't believe this manuscript is unique in taking this approach. I have recently published a paper on how common this approach is and why it doesn't work. I don't want to give the impression that the problem with the analysis was that it was not computationally sophisticated enough or that you did not jump through a specific statistical hoop. If I strip out the arguments that depend on misinterpretations of p-values and -instead- look at the scatterplots, I come up with a very different view of the data than what is described in the paper.

The information in the plots could be translated into a rigorous statistical analysis of estimated differences between groups given the uncertainties of the experimental design. I don't really think that analysis would be useful. I think it would have been enough to publish the plots and report your estimates of the number of active zones in RGCs during development. I don't see evidence of an additional effect.

We appreciate the reviewer’s helpful comments throughout the review process. Mean active zone numbers per mAZ contact are presented in Figure S2D/E. We look forward to further technical and computational advances that will help us increase our data acquisition throughput and sample sizes when designing future studies. 

Reviewer #2 (Recommendations for the authors):

The authors should modify the title and other text to be more consistent with the data. There is no evidence that active zone clustering has any direct relationship to synaptic competition.

We appreciate the reviewer’s helpful suggestions to ensure appropriate language around causal effects. We have modified the title to accurately reflect the results: "Eyespecific differences in active zone addition during synaptic competition in the developing visual system." We have revised the text in the abstract, introduction, and results section for Figures 4 to be consistent with the data and not imply causality of synapse clustering on segregation phenotypes.

Reviewer #3 (Recommendations for the authors):

Change the title.

We appreciate the reviewer’s feedback throughout the review process. We have modified the title to accurately reflect the results: "Eye-specific differences in active zone addition during synaptic competition in the developing visual system."

This section makes me think on the internet nowadays, there's absolutely no way to keep your information to yourself. People's information is in so many different companies, and users would not know how their information is being used either. Users has no control over their own privacy although it's something about themselves.

Author response:

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

Reviewer #1 (Public review):

We thank the reviewer for very enthusiastic and supportive comments on our manuscript. 

Summary:

This manuscript presents a compelling and innovative approach that combines Track2p neuronal tracking with advanced analytical methods to investigate early postnatal brain development. The work provides a powerful framework for exploring complex developmental processes such as the emergence of sensory representations, cognitive functions, and activity-dependent circuit formation. By enabling the tracking of the same neurons over extended developmental periods, this methodology sets the stage for mechanistic insights that were previously inaccessible.

Strengths:

(1) Innovative Methodology:

The integration of Track2p with longitudinal calcium imaging offers a unique capability to follow individual neurons across critical developmental windows.

(2) High Conceptual Impact:

The manuscript outlines a clear path for using this approach to study foundational developmental questions, such as how early neuronal activity shapes later functional properties and network assembly.

(3) Future Experimental Potential:

The authors convincingly argue for the feasibility of extending this tracking into adulthood and combining it with targeted manipulations, which could significantly advance our understanding of causality in developmental processes.

(4) Broad Applicability:

The proposed framework can be adapted to a wide range of experimental designs and questions, making it a valuable resource for the field.

Weaknesses:

No major weaknesses were identified by this reviewer. The manuscript is conceptually strong and methodologically sound. Future studies will need to address potential technical limitations of long-term tracking, but this does not detract from the current work's significance and clarity of vision.

Reviewer #2 (Public review):

Summary:

The manuscript by Majnik and colleagues introduces "Track2p", a new tool designed to track neurons across imaging sessions of two-photon calcium imaging in developing mice. The method addresses the challenge of tracking cells in the growing brain of developing mice. The authors showed that "Track2p" successfully tracks hundreds of neurons in the barrel cortex across multiple days during the second postnatal week. This enabled the identification of the emergence of behavioral state modulation and desynchronization of spontaneous network activity around postnatal day 11.

Strengths:

The manuscript is well written, and the analysis pipeline is clearly described. Moreover, the dataset used for validation is of high quality, considering the technical challenges associated with longitudinal two-photon recordings in mouse pups. The authors provide a convincing comparison of both manual annotation and "CellReg" to demonstrate the tracking performance of "Track2p". Applying this tracking algorithm, Majnik and colleagues characterized hallmark developmental changes in spontaneous network activity, highlighting the impact of longitudinal imaging approaches in developmental neuroscience. Additionally, the code is available on GitHub, along with helpful documentation, which will facilitate accessibility and usability by other researchers.

Weaknesses:

(1) The main critique of the "Track2p" package is that, in its current implementation, it is dependent on the outputs of "Suite2p". This limits adoption by researchers who use alternative pipelines or custom code. One potential solution would be to generalize the accepted inputs beyond the fixed format of "Suite2p", for instance, by accepting NumPy arrays (e.g., ROIs, deltaF/F traces, images, etc.) from files generated by other software. Otherwise, the tool may remain more of a useful add-on to "Suite2p" (see https://github.com/MouseLand/suite2p/issues/933) rather than a fully standalone tool.

We thank the reviewer for this excellent suggestion. 

We have now implemented this feature, where Track2p is now compatible with ‘raw’ NumPy arrays for the three types of inputs. For more information, please check the updated documentation: https://track2p.github.io/run_inputs_and_parameters.html#raw-npy-arrays. We have also tested this feature using a custom segmentation and trace extraction pipeline using Cellpose for segmentation.

(2) Further benchmarking would strengthen the validation of "Track2p", particularly against "CaIMaN" (Giovannucci et al., eLife, 2019), which is widely used in the field and implements a distinct registration approach.

This reviewer suggested  further benchmarking of Track2P.  Ideally, we would want to benchmark Track2p against the current state-of-the-art method. However, the field currently lacks consensus on which algorithm performs best, with multiple methods available including CaIMaN, SCOUT (Johnston et al. 2022), ROICaT (Nguyen et al. 2023), ROIMatchPub (recommended by Suite2p documentation and recently used by Hasegawa et al. 2024), and custom pipelines such as those described by Sun et al. 2025. The absence of systematic benchmarking studies—particularly for custom tracking pipelines—makes it impossible to identify the current state-of-the-art for comparison with Track2p. While comparing Track2p against all available methods would provide comprehensive evaluation, such an analysis falls beyond the scope of this paper.

We selected CellReg for our primary comparison because it has been validated under similar experimental conditions—specifically, 2-photon calcium imaging in developing hippocampus between P17-P25 (Wang et al. 2024)—making it the most relevant benchmark for our developmental neocortex dataset.

That said, to support further benchmarking in mouse neocortex (P8-P14), we will publicly release our ground truth tracking dataset.

(3) The authors might also consider evaluating performance using non-consecutive recordings (e.g., alternate days or only three time points across the week) to demonstrate utility in other experimental designs.

Thank you for your suggestion. We have performed a similar analysis prior to submission, but we decided against including it in the final manuscript, to keep the evaluation brief and to not confuse the reader with too many different evaluation methods. We have included the results inAuthor response images 1 and 2 below.

To evaluate performance in experimental designs with larger time spans between recordings (>1 day) we performed additional evaluation of tracking from P8 to each of the consecutive days while omitting the intermediate days (e. g. P8 to P9, P8 to P10 … P8 to P14). The performance for the three mice from the manuscript is shown below:

Author response image 1.

As expected with increasing time difference between the two recordings the performance drops significantly (dropping to effectively zero for 2 out of 3 mice). This could also explain why CellReg struggles to track cells across all days, since it takes P8 as a reference and attempts to register all consecutive days to that time point before matching, instead of performing registration and matching in consecutive pairs of recordings (P8-P9, P9-P10 … P13-P14) as we do.

Finally for one of the three mice we also performed an additional test where we asked how adding an additional recording day might rescue the P8-P14 tracking performance. This corresponds to the comment from the reviewer, answering the question if we can only perform three days of recording which additional day would give the best tracking performance. 

Author response image 2.

As can be seen from the plot, adding the P10 or P11 recording shows the most significant improvement to the tracking performance, however the performance is still significantly lower than when including all days (see Fig. 4). This test suggests that including a day that is slightly skewed to earlier ages might improve the performance more than simply choosing the middle day between the two extremes. This would also be consistent with the qualitative observation that the FOV seems to show more drastic day-to-day changes at earlier ages in our recording conditions.

Reviewer #3 (Public review):

Summary:

In this manuscript, Majnik et al. developed a computational algorithm to track individual developing interneurons in the rodent cortex at postnatal stages. Considerable development in cortical networks takes place during the first postnatal weeks; however, tools to study them longitudinally at a single-cell level are scarce. This paper provides a valuable approach to study both single-cell dynamics across days and state-driven network changes. The authors used Gad67Cre mice together with virally introduced TdTom to track interneurons based on their anatomical location in the FOV and AAVSynGCaMP8m to follow their activity across the second postnatal week, a period during which the cortex is known to undergo marked decorrelation in spontaneous activity. Using Track2P, the authors show the feasibility of tracking populations of neurons in the same mice, capturing with their analysis previously described developmental decorrelation and uncovering stable representations of neuronal activity, coincident with the onset of spontaneous active movement. The quality of the imaging data is compelling, and the computational analysis is thorough, providing a widely applicable tool for the analysis of emerging neuronal activity in the cortex. Below are some points for the authors to consider.

We thank the reviewer for a constructive and positive evaluation of our MS. 

Major points:

(1) The authors used 20 neurons to generate a ground truth dataset. The rationale for this sample size is unclear. Figure 1 indicates the capability to track ~728 neurons. A larger ground truth data set will increase the robustness of the conclusions.

We think this was a misunderstanding of our ground truth dataset analysis which included 192 and not 20 neurons. Indeed, as explained in the methods section, since manually tracking all cells would require prohibitive amounts of time, we decided to generate sparse manual annotations, only tracking a subset of all cells from the first recording day onwards. To do this, we took the first recording (s0), and we defined a grid 64 equidistant points over the FOV and, for each point, identified the closest ROI in terms of euclidean distance from the median pixel of the ROI (see Fig. S3A). We then manually tracked these 64 ROIs across subsequent days. Only neurons that were detected and tracked across all sessions were taken into account and referred to as our ground truth dataset (‘GT’ in Fig. 4). This was done for 3 mice, hence 3X64 neurons and not 20 were used to generate our GT dataset. 

(2) It is unclear how movement was scored in the analysis shown in Figure 5A. Was the time that the mouse spent moving scored after visual inspection of the videos? Were whisker and muscle twitches scored as movement, or was movement quantified as the amount of time during which the treadmill was displaced?

Movement was scored using a ‘motion energy’ metric as in Stringer et al. 2019 (V1) or Inácio et al. 2025 (S1). This metric takes each two consecutive frames of the videography recordings and computes the difference between them by summing up the square of pixelwise differences between the two images. We made the appropriate changes in the manuscript to further clarify this in the main text and methods in order to avoid confusion.

Since this metric quantifies global movements, it is inherently biased to whole-body movements causing more significant changes in pixel values around the whole FOV of the camera. Slight twitches of a single limb, or the whisker pad would thus contribute much less to this metric, since these are usually slight displacements in a small region of the camera FOV. Additionally, comparing neural activity across all time points (using correlation or R²) also favours movements that last longer (such as wake movements / prolonged periods of high arousal) since each time point is treated equally.

As we suggested in the discussion, in further analysis it would be interesting to look at the link between twitches and neural activity, but this would likely require extensive manual scoring. We could then treat movements not as continuous across all time-points, but instead using event-based analysis for example peri-movement time histograms for different types of movements at different ages, which is however outside of the scope of this study.

(3) The rationale for binning the data analysis in early P11 is unclear. As the authors acknowledged, it is likely that the decoder captured active states from P11 onwards. Because active whisking begins around P14, it is unlikely to drive this change in network dynamics at P11. Does pupil dilation in the pups change during locomotor and resting states? Does the arousal state of the pups abruptly change at P11?

We agree that P11 does not match any change in mouse behavior that we have been able to capture. However, arousal state in mice does change around postnatal day 11. This period marks a transition from immature, fragmented states to more organized and regulated sleep-wake patterns, along with increasing influence from neuromodulatory and sensory systems. All of these changes have been recently reviewed in Wu et al. 2024 (see also Martini et al. 2021). In addition, in the developing somatosensory system, before postnatal day 11 (P11), wake-related movements (reafference) are actively gated and blocked by the external cuneate nucleus (ECN, Tiriac et al. 2016 and all excellent recent work from the Blumberg lab). This gating prevents sensory feedback from wake movements from reaching the cortex, ensuring that only sleep-related twitches drive neural responses. However, around P11, this gating mechanism abruptly lifts, enabling sensory signals from wake movements to influence cortical processing—signaling a dramatic developmental shift from Wu et al. 2024

Reviewer #1 (Recommendations for the authors):

This manuscript represents a significant advancement in the field of developmental neuroscience, offering a powerful and elegant framework for longitudinal cellular tracking using the Track2p method combined with robust analytical approaches. The authors convincingly demonstrate that this integrated methodology provides an invaluable template for investigating complex developmental processes, including the emergence of sensory representations and higher cognitive functions.

A major strength of this work is its emphasis on the power of longitudinal imaging to illuminate activity-dependent development. By tracking the same neurons over time, the authors open up new possibilities to uncover how early activity patterns shape later functional outcomes and the organization of neuronal assemblies-insights that would be inaccessible using conventional cross-sectional designs.

Importantly, the manuscript highlights the potential for this approach to be extended even further, enabling continuous tracking into adulthood and thus offering an unprecedented window into long-term developmental trajectories. The authors also underscore the exciting opportunity to incorporate targeted perturbation experiments, allowing researchers to causally link early circuit dynamics to later outcomes.

Given the increasing recognition that early postnatal alterations can underlie the etiology of various neurodevelopmental disorders, this work is especially timely. The methods and perspectives presented here are poised to catalyze a new generation of developmental studies that can reveal mechanistic underpinnings of both typical and atypical brain development.

In summary, this is a technically impressive and conceptually forward-looking study that sets the stage for transformative advances in developmental neuroscience.

Thank you for the thoughtful feedback—it's greatly appreciated!

Reviewer #2 (Recommendations for the authors):

Minor points:

(1) Figure 1. Consider merging or moving to Supplemental, as its rationale is well described in the text.

We would like to retain the current figure as we believe it provides an effective visual illustration of our rationale that will capture readers' attention and could serve as a valuable reference for others seeking to justify longitudinal tracking of the developing brain. We hope the reviewer will understand our decision.

(2) Some axis labels and panels are difficult to read due to small font sizes (e.g. smaller panels in Figures 5-7).

Modified, thanks 

(3) Supplementary Figures. The order of appearance in the main text is occasionally inconsistent.

This was modified, thanks

(4) Line 132. Add a reference to the registration toolbox used (elastix). A brief description of the affine transformation would also be helpful, either here or in the Methods section (p. 27).

We have added reference to Ntatsis et al. 2023 and described affine transformation in the main text (lines 133-135): 

Firstly, we estimate the spatial transformation between s0 and s1 using affine image registration (i.e. allowing shifting, rotation, scaling and shearing, see Fig. 2B, the transformation is denoted as T).

(5) Lines 147-151. If this method is adapted from another work, please cite the source.

Computing the intersection over union of two ROIs for tracking is a widely established and intuitive method used across numerous studies, representing standard practice rather than requiring specific citation. We have however included the reference to the paper describing the algorithm we use to solve the linear sum assignment problem used for matching neurons across a pair of consecutive days (Crouse 2016).

(6) Line 218. "classical" or automatic?

We meant “classical” in the sense of widely used. 

(7) Lines 220-231. Did the authors find significant variability of successfully tracked neurons across mice? While the data for successfully tracked cells is reported (Figure 5B), the proportions are not. Could differences in neuron dropout across days and mice affect the analysis of neuronal activity statistics?

We thank the reviewer for raising this important point. We computed the fraction of successfully tracked cells in our dataset and found substantial variability:

Cells detected on day 0: [607, 1849, 2190, 1988, 1316, 2138] 

Proportion successfully tracked: [0.47, 0.20, 0.36, 0.37, 0.41, 0.19]

Notably, the number of cells detected on the first day varies considerably (607–2138 cells). There appears to be a trend whereby datasets with fewer initially detected cells show higher tracking success rates, potentially because only highly active cells are identified in these cases.

To draw more definitive conclusions about the proportion of active cells and tracking dropout rates, we would require activity-independent cell detection methods (such as Cellpose applied to isosbestic 830 nm fluorescence, or ideally a pan-neuronal marker in a separate channel, e.g., tdTomato). We have incorporated the tracking success proportions into the revised manuscript.

(8) Line 260. Please briefly explain, here or in the Methods, the rationale for using data from only 3 mice (rather than all 6) for evaluating tracking performance.

We used three mice for this analysis due to the labor-intensive nature of manually annotating 64 ROIs across several days. Given the time constraints of this manual process, we determined that three subjects would provide adequate data to reliably assess tracking performance.

(9) Line 277. Consider clarifying or rephrasing the phrase "across progressively shorter time intervals"? Do you mean across consecutive days?

This has been rephrased as follows: 

Additionally, to assess tracking performance over time, we quantified the proportion of reconstructed ground truth tracks over progressively longer time intervals (first two days, first three days etc. ‘Prop. correct’ in Fig. 4C-F, see Methods). This allowed us to understand how tracking accuracy depends on the number of successive sessions, as well as at which time points the algorithm might fail to successfully track cells.

(10) Line 306. "we also provide additional resources and documentation". Please add a reference or link.

Done, thanks

Track2p  

(11) Lines 342-344. Specify that the raster plots refer to one example mouse, not the entire sample.

Done, thanks.

(12) Lines 996-1002. Please confirm whether only successfully tracked neurons were used to compute the Pearson correlations between all pairs.

Yes of course, this only applies to tracked neurons as it is impossible to compute this for non-tracked pairs.

(13) Line 1003. Add a reference to scikit-learn.

Reference was added to: 

Pedregosa, F., Varoquaux, G., Gramfort, A., Michel, V., Thirion, B., Grisel, O., Blondel, M., Prettenhofer, P., Weiss, R., Dubourg, V., Vanderplas, J., Passos, A., Cournapeau, D., Brucher, M., Perrot, M., & Duchesnay, E. (2011). Scikit-learn: Machine Learning in Python. Journal of Machine Learning Research, 12, 2825–2830. 

(14) Typos.Correct spacing between numeric values and units.

We did not find many typos regarding spacing between the numerical value and the unit symbol (degrees and percent should not be spaced right?).

Reviewer #3 (Recommendations for the authors):

The font size in many of the figures is too small. For example, it is difficult to follow individual ROIs in Figure S3.

Figure font size has been increased, thanks. In Figure S3 there might have been a misunderstanding, since the three FOV images do not correspond to the FOV of the same mouse across three days but rather to the first recording for each of the three mice used in evaluation (the ROIs can thus not be followed across images since they correspond to a different mouse). To avoid confusion we have labelled each of the FOV images with the corresponding mouse identifier (same as in Fig. 4 and 5).

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

Summary: 

In this manuscript, the authors explore the role of the conserved transcription factor POU4-2 in planarian maintenance and regeneration of mechanosensory neurons. The authors explore the role of this transcription factor and identify potential targets of this transcription factor. Importantly, many genes discovered in this work are deeply conserved, with roles in mechanosensation and hearing, indicating that planarians may be a useful model with which to study the roles of these key molecules. This work is important within the field of regenerative neurobiology, but also impactful for those studying the evolution of the machinery that is important for human hearing. 

Strengths: 

The paper is rigorous and thorough, with convincing support for the conclusions of the work. 

Weaknesses: 

Weaknesses are relatively minor and could be addressed with additional experiments or changes in writing.

Reviewer #2 (Public review): 

Summary: 

In this manuscript, the authors investigate the role of the transcription factor Smed-pou4-2 in the maintenance, regeneration, and function of mechanosensory neurons in the freshwater planarian Schmidtea mediterranea. First, they characterize the expression of pou4-2 in mechanosensory neurons during both homeostasis and regeneration, and examine how its expression is affected by the knockdown of soxB1, 2, a previously identified transcription factor essential for the maintenance and regeneration of these neurons. Second, the authors assess whether pou4-2 is functionally required for the maintenance and regeneration of mechanosensory neurons. 

Strengths: 

The study provides some new insights into the regulatory role of pou4-2 in the differentiation, maintenance, and regeneration of ciliated mechanosensory neurons in planarians. 

Weaknesses: 

The overall scope is relatively limited. The manuscript lacks clear organization, and many of the conclusions would benefit from additional experiments and more rigorous quantification to enhance their strength and impact. 

Reviewing Editor Comments: 

(1) Quantification of pou4-2(+) cells that express (or do not express) hmcn-1-L and/or pkd1L-2(-) is a common suggestion amongst reviewers. It is recognized that Ross et al. (2018) showed that pkd1L-2 and hmcn-1L expression is detected in separate cells by double FISH, and the analysis presented in Supplementary Figure S3 is helpful in showing that some cells expressing pou4-2 (magenta) are not labeled by the combined signal of pkd1L-2 and hmcn-1-L riboprobes (green). However, I am not sure that we can conclude that pkd1L-2 and hmcn-1-L are effectively detected when riboprobes are combined in the analysis. Therefore, quantification of labeled cells as proposed by Reviewers 1 and 2 would help.

Combining riboprobes is a standard approach in the field, and we chose this method as a direct way to determine which cells lack expression of both genes. We agree that providing the raw quantification data would be helpful for readers, and we included this data in Supplementary File S7; the file contains the quantification information for this dFISH experiment represented in Supplementary Figure 3.

(2) It may be helpful to comment on changes (or lack of changes) in atoh gene RNA levels in RNAseq analyses of pou4-2 animals. As mentioned by one of the reviewers, in situs that don't show signal are inconclusive in this regard. 

We fully agree with both reviewers. Two of the planarian atonal homologs are difficult to detect and produce background signals, which we attempted and previously reported in Cowles et al. Development (2013). We conceived performing reciprocal RNAi/in situ experiments, born out of curiosity given the reported role of atonal in the pou4 cascade in other organisms. However, these exploratory experiments lacked a strong rationale for inclusion, particularly given that pou4-2 and the atonal homologs do not share expression patterns, co-expression, or differential expression in our RNA-seq dataset. Therefore, we decided to omit the atonal in situs following pou4-2 RNAi. We retained the experiments showing that knockdown of the atonal genes does not show robust effects on the mechanosensory neuron pattern, as expected. We thank the reviewing editor and reviewers for pinpointing the concern. We agree that additional experiments, such as qPCR experiments, would be needed. We reasoned that while these additional experiments could be informative, they are unlikely to alter the key conclusions of this study substantially.

(3) There seem to be typos at bottom of Figure 10 and top of page 11 when referencing to Figure 4B (should be to 5B instead): "While mechanosensory neuronal patterned expression of Eph1 was downregulated after pou4-2 and soxB1-2 inhibition, low expression in the brain branches of the ventral cephalic ganglia persisted (Figure 4B)." 

Thank you! We have fixed those.

(4) Typo (page 13; kernel?): "...to test to what extent the Pou4 gene regulatory kernel is conserved among these widely divergent animals." 

Regulatory kernels are defined as the minimal sets of interacting genes that drive developmental processes and are the core circuits within a gene regulatory network, but we recognize that this might not be as well known, so we have changed the term to “network” for clarity.

Reviewer #1 (Recommendations for the authors): 

(1) The authors indicate that they are interested in finding out whether POU4-2 is important in the creation of mechanosensory neurons in adulthood as well as in embryogenesis (in other words, whether the mechanism is "reused during adult tissue maintenance and regeneration"). The manuscript clearly shows that planarian POU4 -2 is important in adult neurogenesis in planarians, but there is no evidence presented to show that this is a recapitulation of embryogenesis. Is pou4-2 expressed in the planarian embryo? This might be possible to examine by ISH or through the evaluation of sequencing data that already exists in the literature. 

We agree that these statements should be precise. We have clarified when we make comparisons to the role of Pou4 in sensory system development in other organisms versus its role in the adult planarian. We examined its expression using the existing database of embryonic gene expression. Thanks for hinting at this idea. We performed BLAST in Planosphere (Davies et al., 2017) to cross-reference our clone matching dd_Smed_v6_30562_0_1, which is identical to SMED30002016. The embryonic gene expression for SMED30002016 indicates this gene is expressed at the expected stages given prior knowledge of the timing of organ development in Schmidtea mediterranea (a positive trend begins at Stage 5, with a marked increase by Stage 6 that remains comparable to the asexual expression levels shown). We thank the reviewer for pointing out this oversight. We have incorporated this result in the paper as a Supplementary Figure and discuss how we can only speculate that it has a similar role as we detect in the adult asexual worms.

(2) Can it be determined whether the punctate pou4-2+ cells outside of the stripes are progenitors or other neural cell types? Are there pou4-2+ neurons that are not mechanosensory cell types? Could there be other roles for POU4-2 in the neurogenesis of other cell types? It might help to show percentages of overlap in Figure 4A and discuss whether the two populations add up to 100% of cells. 

These are good questions that arise in part from other statements that need clarification in the text (pointed out by Reviewer 2). We think some of the dorsal pou4-2⁺ might represent progenitor cells undergoing terminal differentiation (see Supplementary Figure 4). We attempted BrdU pulse chase experiments but were not successful in consistently detecting pou4-2 at sufficient levels with our protocol. In response to this helpful comment, we have included this question as a future direction in the revised Discussion. Finally, we have edited our description of the expression pattern. We already pointed out that there are other cells on the ventral side that are not affected when soxB1-2 is knocked down. We attempted to resolve the potential identity of those cells working with existing scRNA-seq data in collaboration with colleagues, but their low abundance made it difficult to distinguish other populations. While we acknowledge this interesting possibility, we have chosen to focus this report on the role of pou4-2 downstream of soxB1-2, as this represents the most well-supported aspect of the dataset and was positively highlighted by both the reviewer and editor.

(3) The authors discuss many genes from their analysis that play conserved roles in mechanosensation and hearing. Were there any conserved genes that came up in the analysis of pou4-2(RNAi) planarians that have not yet been studied in human hearing and neurodevelopment? I am wondering the extent to which planarians could be used as a discovery system for mechanosensory neuron function and development, and discussion of this point might increase the impact of this paper or provide critical rationale for expanding work on planarian mechanosensation. 

Indeed, we agree that planarians could be used to identify conserved genes with roles in mechanosensation and have included this point in the Discussion. In this study, we have focused on demonstrating the conservation of gene regulation. While this study was initially based on a graduate thesis project, we have since generated a more comprehensive dataset from isolated heads, which we are currently analyzing. This has been emphasized in the revised Discussion.

Minor: 

(1) For Figure 6E, the authors could consider showing data along a negative axis to indicate a decrease in length in response to vibration and to more clearly show that this decrease doesn't occur as strongly after pou4-2(RNAi). 

We displayed this behavior as the percent change, as this is a standard way to represent this data. As the percent change is a positive value, we represent the data as these positive values.

(2) The authors should consider quantifying the decrease of pou4-2 mRNA after atonal(RNAi) conditions, either by RT-qPCR or cell quantification. Visually, the signal in the stripes after atoh8-2(RNAi) seems lower, particularly in the tail. The punctate pattern outside the stripes may also be decreased after atoh8-1(RNAi). But quantification might strengthen the argument. 

We agree with the reviewer and acknowledge that we should have been more cautious in interpreting these results. Those two genes are difficult to detect and did not show specific patterns in Cowles et al. (2013). The reviewer is correct that additional experiments are necessary before reaching conclusions, but we do not think as discussed earlier we do not think new experiments would provide insights for the major conclusions. These experiments were exploratory in nature and tangential to our main conclusions, especially in the absence of reciprocal evidence (e.g., shared expression patterns, co-expression, or differential expression in our RNA-seq data. Therefore, we decided to eliminate the atonal in situs following pou4-2 RNAi.

Reviewer #2 (Recommendations for the authors): 

A. Expression of pou4-2 in ciliated mechanosensory neurons: 

(1) The conclusion that pou4-2 is expressed in ciliated mechanosensory neurons is primarily based on co-expression analysis using a published single-cell dataset. Although the authors later show that a subset of pou4-2 cells also express pkd1L-2 (Figure 4A), a known marker of ciliated mechanosensory neurons, this finding is not properly quantified. I recommend moving Figure 4A to earlier in the manuscript (e.g., to Figure 2) and expanding the analysis to include additional known markers of this cell type. Proper quantification of the extent of co-localization is necessary to support the claim robustly. 

As pointed out by the reviewer, there is substantive evidence from our lab and other reports. King et al. also showed pou4-2 and pkd1L-2 ‘regulation’ by their scRNA-seq data, and this function is conserved in the acoel Hofstenia miamia (Hulett et al., PNAS 2024 ). Our analysis shows convincing co-localization by scRNA-seq and expression of soxB1-2 and neural markers in the respective populations. Furthermore, we included colocalization of pou4-2 with mechanosensory genes using fluorescence in situ hybridization (Figure 3B, Supplementary Figure 4, and Supplementary File S7). We are confident the data conclusively show pou4-2 regulates pkd1L-2 expression in a subset of mechanosensory neurons. Given the strength of existing observations and previously published data, we believe that additional staining experiments are not essential to support this conclusion. 

(2) There appears to be a conceptual inconsistency in the interpretation of pou4-2 expression dynamics. On one hand, the authors suggest that delayed pou4-2 expression indicates a role in late-stage differentiation (p.6). On the other hand, they propose that pou4-2 may be expressed in undifferentiated progenitors to initiate downstream transcriptional programs (p.8). These interpretations should be reconciled. Additionally, claims regarding pou4-2 expression in progenitor populations should be supported by co-localization with established stem cell or progenitor markers, rather than inferred from signal intensity alone. 

This is an excellent point, and we agree with the reviewer that this section requires editing. As described in response to Reviewer 1, we attempted BrdU pulse chase experiments but were not successful in consistently detecting pou4-2 at sufficient levels with our protocol. Furthermore, we could not obtain strong signals in double labeling experiments in pou4-2 in situs combined with piwi-1 or PIWI-1 antibodies. We will include those experiments as a future direction and amend our conclusions accordingly.

(3) The expression pattern shown in Figure 1B raises questions about the precise anatomical localization of pou4-2 cells. It is unclear whether these cells reside in the subepidermal plexus or the deeper submuscular plexus, which represent distinct neuronal layers (Ross et al., 2017). The observed signals near the ventral nerve cords could suggest submuscular localization. To clarify this, higher-resolution imaging and co-staining with region-specific neural markers are recommended. 

In Ross et al. (2018), we showed that the pkd1L-2⁺ cells are located submuscularly. The pkd1L-2 cells express pou4-2, thus the pou4-2⁺ cells are located in the same location. Based on co-expression data and co-expression with PKD genes, we are confident it is submuscular.

B. The functional requirements of pou4-2 in the maintenance of mechanosensory neurons: 

(1) To evaluate the functional role of pou4-2 in maintaining mechanosensory neurons, the authors performed whole-animal RNA-seq on pou4-2(RNAi) and control animals, identifying a significant downregulation of genes associated with mechanosensory neuron expression. However, the presentation of these findings is fragmented across Figures 3, 4, and 5. I recommend consolidating the RNA-seq results (Figure 3) and the subsequent validation of downregulated genes (Figures 4 and 5) into a single, cohesive figure. This would improve the logical flow and clarity of the manuscript. 

As suggested by the reviewer, we have combined Figures 3 and 4 (new Figure 3), which we believe improves the flow. We decided to keep Figure 5 (new Figure 4) as a standalone because it focuses on the characterization of new genes revealed by RNAseq and scRNA-seq data mining that were not previously reported in Ross et al. 2018 and

2024.

(2) In pou4-2(RNAi) animals, pkd1L-2 expression appears to be entirely lost, while hmcn-1-L shows faint expression in scattered peripheral regions. The authors suggest that an extended RNAi treatment might be necessary to fully eliminate hmcn-1-L expression. However, an alternative explanation is that pou4-2 is not essential for maintaining all hmcn-1-L cells, particularly if pou4-2 expression does not fully overlap with that of hmcn-1-L. This possibility should be acknowledged and discussed. 

We agree and have acknowledged this point in the revised text.

(3) On page 9, the section title claims that "Smed-pou4-2 regulates genes involved in ciliated cell structure organization, cell adhesion, and nervous system development." While some differentially expressed genes are indeed annotated with these functions based on homology, the manuscript does not provide experimental evidence supporting their roles in these biological processes in planarians. The title should be revised to avoid overstatement, and the limitations of extrapolating a function solely from gene annotation should be acknowledged. 

Excellent point. We have edited the text to indicate that the genes were annotated or implicated.

(4) The cilia staining presented in Figure 6B to support the claim that pou4-2 is required for ciliated cell structure organization is unconvincing. Improved imaging and more targeted analysis (e.g., co-labeling with mechanosensory markers) are needed to support this conclusion. 

We have addressed this concern by adjusting the language to be more precise and indicate that the stereotypical banded pattern is disrupted with decreased cilia labeling along the dorsal ciliated stripe. Indeed, our conclusion overstated the observations made with the staining and imaging resolution. Thank you.

C. The functional requirements of pou4-2 in the regeneration of mechanosensory neurons: 

To evaluate the role of pou4-2 in the regeneration of mechanosensory neurons, the authors performed amputations on pou4-2(RNAi) and control(RNAi) animals and assessed the expression of mechanosensory markers (pkd1L-2, hmcn-1-L) alongside a functional assay. However, the results shown in Figure 4B indicate the presence of numerous pkd1L-2 and hmcn-1-L cells in the blastema of pou4-2(RNAi) animals. This observation raises the possibility that pou4-2 may not be essential for the regeneration of these mechanosensory neurons. The authors should address this alternative interpretation. 

Our interpretation is that there were very few cells expressing the markers compared to controls. The pattern was predominantly lost, which is consistent with other experiments shown in the paper. However, we have added the additional caveat suggested by the reviewer.

Minor points: 

(1) On p.8, the authors wrote "every 12 hours post-irradiation". However, this is not consistent with the figure, which only shows 0, 3, 4, 4.5, 5, and 5.5 dpi. 

We corrected this. Thank you for catching the mistake!

(2) On p.12, the authors wrote "Analysis of pou4-2 RNAi data revealed differentially expressed genes with known roles in mechanosensory functions, such as loxhd-1, cdh23, and myo7a. Mutations in these genes can cause a loss of mechanosensation/transduction". This is misleading because, to my knowledge, the role of these genes in planarians is unknown. If the authors meant other model systems, they should clearly state this in the text and include proper references. 

The reviewer is correct that we are referencing findings from other organisms. We have clarified this point in the revised text. The appropriate references were included and cited in the first version.

(3) On p.7, the authors wrote, "conversely, the expression of atonal genes was unaffected in pou4-2 RNAi-treated regenerates (Supplementary Figure S2B)". However, it is unclear whether the Atoh8-1 and Atoh8-2 signals are real, as the quality of the in situ results is too low to distinguish between real signals and background noise/non-specific staining. 

This valid concern was addressed in our response to Reviewer 1. We have adjusted the figure and the text accordingly.

(4) On p.6 the authors wrote "pinpointed time points wherein the pou4-2 transcripts were robustly downregulated". However, the current version of the manuscript does not provide data explaining why Pou4-2 transcripts are robustly downregulated on day 12. 

Yes, we determined the appropriate time points using qPCR for all sample extractions. As an example, see the figure for qPCR validation at day 12 showing that pou4-2 and pkd1L2 are down.

Author response image 1.

In this graph, samples labeled “G” represent four biological controls of gfp(RNAi) control animals, and samples labeled “P” represent four biological controls of pou4-2(RNAi)animals at day 12 in the RNAi protocol.

(5) On p.13, the authors wrote "collecting RNA from how animals." Is this a typo? 

Thanks for catching the typo. It should read “whole” animals. We have corrected this.

(6) On p.14, the authors wrote "but the expression patterns of planarian atonal genes indicated that they represent completely different cell populations from pou4-2-regulated mechanosensory neurons". However, this is unclear from the images, as the in situ staining of Atoh8-1 and Atoh82 are potentially failed stainings. 

We agree. We have edited accordingly.

Author response:

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

Reviewer #1 (Public review):

Summary:

The manuscript "Lifestyles shape genome size and gene content in fungal pathogens" by Fijarczyk et al. presents a comprehensive analysis of a large dataset of fungal genomes to investigate what genomic features correlate with pathogenicity and insect associations. The authors focus on a single class of fungi, due to the diversity of lifestyles and availability of genomes. They analyze a set of 12 genomic features for correlations with either pathogenicity or insect association and find that, contrary to previous assertions, repeat content does not associate with pathogenicity. They discover that the number of proteincoding genes, including the total size of non-repetitive DNA does correlate with pathogenicity. However, unique features are associated with insect associations. This work represents an important contribution to the attempts to understand what features of genomic architecture impact the evolution of pathogenicity in fungi.

Strengths:

The statistical methods appear to be properly employed and analyses thoroughly conducted. The manuscript is well written and the information, while dense, is generally presented in a clear manner.

Weaknesses:

My main concerns all involve the genomic data, how they were annotated, and the biases this could impart to the downstream analyses. The three main features I'm concerned with are sequencing technology, gene annotation, and repeat annotation.

We thank the reviewer for all the comments. We are aware that the genome assemblies are of heterogeneous quality since they come from many sources. The goal of this study was to make the best use of the existing assemblies, with the assumption that noise introduced by the heterogeneity of sequencing methods should be overcome by the robustness of evolutionary trends and the breadth and number of analyzed assemblies. Therefore, at worst, we would expect a decrease in the power to detect existing trends. It is important to note that the only way to confidently remove all potential biases would be to sequence and analyze all species in the same way; this would require a complete study and is beyond the scope of the work presented here. Nevertheless some biases could affect the results in a negative way, eg. is if they affect fungal lifestyles differently. We therefore made an attempt to explore the impact of sequencing technology, gene and repeat annotation approach among genomes of different fungal lifestyles. Details are described in Supplementary Results and below. Overall, even though the assembly size and annotations conducted with Augustus can sometimes vary compared to annotations from other resources, such as JGI Mycocosm, we do not observe a bias associated with fungal lifestyles. Comparison of annotations conducted with Augustus and JGI Mycocosm dataset revealed variation in gene-related features that reflect biological differences rather than issues with annotation.  

The collection of genomes is diverse and includes assemblies generated from multiple sequencing technologies including both short- and long-read technologies. Not only has the impact of the sequencing method not been evaluated, but the technology is not even listed in Table S1. From the number of scaffolds it is clear that the quality of the assemblies varies dramatically. This is going to impact many of the values important for this study, including genome size, repeat content, and gene number.

We have now added sequencing technology in Table S1 as it was reported in NCBI. We evaluated the impact of long-read (Nanopore, PacBio, Sanger) vs short-read assemblies in Supplementary Results. In short, the proportion of different lifestyles (pathogenic vs. nonpathogenic, IA vs non-IA) were the same for short- and long-read assemblies. Indeed, longread assemblies were longer, had a higher fraction of repeats and less genes on average, but the differences between pathogenic vs. non-pathogenic (or IA vs non-IA) species were in the same direction for two sequencing technologies and in line with our results. There were some discrepancies, eg. mean intron length was longer for pathogens with long-read assemblies, but slightly shorter on average for short-read assemblies (and to lesser extent GC and pseudo tRNA count), which could explain weaker or mixed results in our study for these features.

Additionally, since some filtering was employed for small contigs, this could also bias the results.

The reason behind setting the lower contig length threshold was the fact that assemblies submitted to NCBI have varying lower-length thresholds. This is because assemblers do not output contigs above a certain length, and this threshold can be manipulated by the user. Setting a common min contig length was meant to remove this variation, knowing that any length cut-off will have a larger effect on short-read based assemblies than long-read-based assemblies. Notably, genome assemblies of corresponding species in JGI Mycocosm have a minimum contig length of 865 bp, not much lower than in our dataset. Importantly, in a response to a comment of previous reviewer, repeat content was recalculated on raw assembly lengths instead of on filtered assembly length. 

I have considerable worries that the gene annotation methods could impart biases that significantly affect the main conclusions. Only 5 reference training sets were used for the Sordariomycetes and these are unequally distributed across the phylogeny. Augusts obviously performed less than ideally, as the authors reported that it under-annotated the genomes by 10%. I suspect it will have performed worse with increasing phylogenetic distance from the reference genomes. None of the species used for training were insectassociated, except for those generated by the authors for this study. As this feature was used to split the data it could impact the results. Some major results rely explicitly on having good gene annotations, like exon length, adding to these concerns. Looking manually at Table S1 at Ophiostoma, it does seem to be a general trend that the genomes annotated with Magnaporthe grisea have shorter exons than those annotated with H294. I also wonder if many of the trends evident in Figure 5 are also the result of these biases. Clades H1 and G each contain a species used in the training and have an increase in genes for example.

We have applied 6 different reference training sets (instead of one) precisely to address the problem of increasing phylogenetic distance of annotated species. To further investigate the impact of chosen species for training, we plotted five gene features (number of genes, number of introns, intron length, exon length, fraction of genes with introns) as a function of   branch length distance from the species (or genus) used as a training set for annotation. We don’t see systematic biases across different training sets. However,  trends are very clear for clades annotated with fusarium. This set of species includes Hypocreales and Microascales, which is indeed unfortunate since Microascales is an IA group and at the same time the most distant from the fusarium genus in this set. To clarify if this trend is related to annotation bias or a biological trend, we compared gene annotations with those of Mycocosm, between Hypocreales Fusarium species, Hypocreales non-Fusarium species, and Microascales, and we observe exactly the same trends in all gene features. 

Similarly, among species that were annotated with magnaporthe_grisea, Ophiostomatales (another IA group) are among the most distant from the training set species. Here, however, another order, Diaporthales, is similarly distant, yet the two orders display different feature ranges. In terms of exon length, top 2 species in this training set include Ophiostoma, and they reach similar exon length as the Ophiostoma species annotated using H294 as a training set. In summary, it is possible that the choice of annotation species has some effect on feature values; however, in this dataset, these biases are likely mitigated by biological differences among lifestyles and clades. 

Unfortunately, the genomes available from NCBI will vary greatly in the quality of their repeat masking. While some will have been masked using custom libraries generated with software like Repeatmodeler, others will probably have been masked with public databases like repbase. As public databases are again biased towards certain species (Fusarium is well represented in repbase for example), this could have significant impacts on estimating repeat content. Additionally, even custom libraries can be problematic as some software (like RepeatModeler) will include multicopy host genes leading to bona fide genes being masked if proper filtering is not employed. A more consistent repeat masking pipeline would add to the robustness of the conclusions.

We have searched for the same species in JGI Mycocosm and were able to retrieve 58 genome assemblies with matching species, with 19 of them belonging to the same strain as in our dataset. Overall we found no differences in genome assembly length. Interestingly, repeat content was slightly higher for NCBI genome assemblies compared to JGI Mycocosm assemblies, perhaps due to masking of host multicopy genes, as the reviewer mentioned. By comparing pathogenic and non-pathogenic species for the same 19 strains, we observe that JGI Mycocosm annotates fewer repeats in pathogenic species than Augustus annotations (but trends are similar when taking into account 58 matching species). Given a small number of samples, it is hard to draw any strong conclusions; however, the differences that we see are in favor of our general results showing no (or negative) correlation of repeat content with pathogenicity. 

To a lesser degree, I wonder what impact the use of representative genomes for a species has on the analyses. Some species vary greatly in genome size, repeat content, and architecture among strains. I understand that it is difficult to address in this type of analysis, but it could be discussed.

In our case the use of protein sequences could underestimate divergence between closely related strains from the same species. We also excluded strains of the same species to avoid overrepresentation of closely related strains with similar lifestyle traits. We agree that some changes in the genome architecture can occur very rapidly, even at the species level, though analyzing emergence of eg. pathogenicity at the population level would require a slightly different approach which accounts for population-level processes. 

Reviewer #2 (Public review):

Summary:

In this paper, the authors report on the genomic correlates of the transition to the pathogenic lifestyle in Sordariomycetes. The pathogenic lifestyle was found to be better explained by the number of genes, and in particular effectors and tRNAs, but this was modulated by the type of interacting host (insect or not insect) and the ability to be vectored by insects.

Strengths:

The main strength of this study lies in the size of the dataset, and the potentially high number of lifestyle transitions in Sordariomycetes.

Weaknesses:

The main strength of the study is not the clarity of the conclusions.

(1) This is due firstly to the presentation of the hypotheses. The introduction is poorly structured and contradictory in some places. It is also incomplete since, for example, fungusinsect associations are not mentioned in the introduction even though they are explicitly considered in the analyses.

We thank the reviewer for pointing this out. We strived to address all comments and suggestions of the reviewer to clarify the message and remove the contradictions. We also added information about why we included insect-association trait in our analysis. 

(2) The lack of clarity also stems from certain biases that are challenging to control in microbial comparative genomics. Indeed, defining lifestyles is complicated because many fungi exhibit different lifestyles throughout their life cycles (for instance, symbiotic phases interspersed with saprotrophic phases). In numerous fungi, the lifestyle referenced in the literature is merely the sampling substrate (such as wood or dung), which doesn't mean that this substrate is a crucial aspect of the life cycle. This issue is discussed by the authors, but they do not eliminate the underlying uncertainties.

We agree with the reviewer that lack of certainty in the lifestyle or range of possible lifestyles of studied species is a weakness in this analysis. We are limited by the information available in the literature. We hope that our study will increase interest in collecting such data in the future.

Reviewer #3 (Public review):

Summary:

This important study combines comparative genomics with other validation methods to identify the factors that mediate genome size evolution in Sordariomycetes fungi and their relationship with lifestyle. The study provides insights into genome architecture traits in this Ascomycete group, finding that, rather than transposons, the size of their genomes is often influenced by gene gain and loss. With an excellent dataset and robust statistical support, this work contributes valuable insights into genome size evolution in Sordariomycetes, a topic of interest to both the biological and bioinformatics communities.

Strengths:

This study is complete and well-structured.

Bioinformatics analysis is always backed by good sampling and statistical methods. Also, the graphic part is intuitive and complementary to the text.

Weaknesses:

The work is great in general, I just had issues with the Figure 1B interpretation.

I struggled a bit to find the correspondence between this sentence: "Most genomic features were correlated with genome size and with each other, with the strongest positive correlation observed between the size of the assembly excluding repeats and the number of genes (Figure 1B)." and the Figure 1B. Perhaps highlighting the key p values in the figure could help.

We thank the reviewer for pointing out this sentence. Perhaps the misunderstanding comes from the fact that in this sentence one variable is missing. The correct version should be “Most genomic features were correlated with genome size and with each other, with the strongest positive correlation observed between the genome size, the genome size excluding repeats and the number of genes (Figure 1B)”. Also, the variable names now correspond better to those shown on the figure.

Reviewer #1 (Recommendations for the authors):

The authors have clearly done a lot of good work, and I think this study is worthwhile. I understand that my concerns about the underlying data could necessitate rerunning the entire analysis with better gene models, but there may be another option. JGI has a fairly standard pipeline for gene and repeat annotation. Their gene predictions are based on RNA data from the sequenced strain and should be quite good in general. One could either compare the annotations from this manuscript to those in mycocosm for genomes that are identical and see if there are systematic biases, or rerun some analyses on a subset of genomes from mycocosm. Indeed, it's possible that the large dataset used here compensates for the above concerns, but without some attempt to evaluate these issues, it's difficult to have confidence in the results.

We very appreciate the positive reception of our manuscript. Following the reviewer’s comments we have investigated gene annotations in comparison with those of JGI Mycocosm, even though only 58 species were matching and only 19 of them were from the same strain. This dataset is not representative of the Sordariomycetes diversity (most species come from one clade), therefore will not reflect the results we obtained in this study. To note, the reason for not choosing JGI Mycocosm in the first place, was the poor representation of the insect-associated species, which we found key in this study. In general, we found that assembly lengths were nearly identical, number of genes was higher, and the repeat content was lower for the JGI Mycocosm dataset. When comparing different lifestyles (in particular pathogens vs. non-pathogens), we found the same differences for our and JGI Mycocosm annotations, with one exception being the repeat content. In the small subset (19 same-strain assemblies), our dataset showed the same level of repeats between the two lifestyles, whereas JGI Mycocosm showed lower repeat content for pathogens (but notably for all 58 species, the trend was same for our and JGI Mycocosm annotations). None of these observations are in conflict with our results where we find no or negative association of repeat content with pathogens. 

The figures are very information-dense. While I accept that this is somewhat of a necessity for presenting this type of study, if the authors could summarize the important information in easier-to-interpret plots, that could help improve readability.

We put a lot of effort into showing these complicated results in as approachable manner as possible. Given that other reviewers find them intuitive we decided to keep most of them as they are. To add more clarification, we added one supplementary figure showing distributions of genomic traits across lifestyles. Moreover, in Figure 5, a phylogenetic tree was added with position of selected clades, as well as a scatterplot showing distributions of mean values for genome size and number of genes for those clades. If the reviewer has any specific suggestions on what to improve and in which figure, we’re happy to consider it. 

Reviewer #2 (Recommendations for the authors):

I have no major comments on the analyses, which have already been extensively revised. My major criticism is the presentation of the background, which is very insufficient to understand the importance or relevance of the results presented fully.

Lines are not numbered, unfortunately, which will not help the reading of my review.

(1) The introduction could better present the background and hypotheses:

(a) After reading the introduction, I still didn't have a clear understanding of the specific 'genome features' the study focuses on. The introduction fails to clearly outline the current knowledge about the genetic basis of the pathogenic lifestyle: What is known, what remains unknown, what constitutes a correlation, and what has been demonstrated? This lack of clarity makes reading difficult.

We thank the reviewer for pointing this out. We have now included in the introduction a list of genomic traits we focus on. We also tried to be more precise about demonstrated pathogenic traits and other correlated traits in the introduction. 

(b) Page 3. « Various features of the genome have been implicated in the evolution of the pathogenic lifestyle. » The cited studies did not genuinely link genome features to lifestyle, so the authors can't use « implicated in » - correlation does not imply causation.

This sentence also somehow contradicts the one at the end of the paragraph: « we still have limited knowledge of which genomic features are specific to pathogenic lifestyle

We thank the reviewer for this comment. We added a phrase “correlated with or implicated in” and changed the last sentence of the paragraph into “Yet we still have limited knowledge of how important and frequent different genomic processes are in the evolution of pathogenicity across phylogenetically distinct groups of fungi and whether we can use genomic signatures left by some of these processes as predictors of pathogenic state.”.

(c) Page 3: « Fungal pathogen genomes, and in particular fungal plant pathogen genomes have been often linked to large sizes with expansions of TEs, and a unique presence of a compartmentalized genome with fast and slow evolving regions or chromosomes » Do the authors really need to say « often »? Do they really know how often?

We removed “often”.

(d) Such accessory genomic compartments were shown to facilitate the fast evolution of effectors (Dong, Raffaele, and Kamoun 2015) ». The cited paper doesn't « show » that genomic compartments facilitate the fast evolution of effectors. It's just an observation that there might be a correlation. It's an opinion piece, not a research manuscript.

We changed the sentence to “Such accessory genomic compartments could facilitate the fast evolution of effectors”.

(e) even though such architecture can facilitate pathogen evolution, it is currently recognized more as a side effect of a species evolutionary history rather than a pathogenicity related trait ». This sentence somehow contradicts the following one: « Such accessory genomic compartments were shown to facilitate the fast evolution of effectors".

Here we wanted to point out that even though accessory genome compartments and TE expansions can facilitate pathogen evolution the origin of such architecture is not linked to pathogenicity. We reformulated the sentence to “Even though such architecture can facilitate pathogen evolution, it is currently recognized that its origin is more likely a side effect of a species evolutionary history rather than being caused by pathogenicity”.

(f) As the number of genes is strongly correlated with fungal genome size (Stajich 2017), such expansions could be a major contributor to fungal genome size. » This sentence suggests that pathogens might have bigger genomes because they have more effectors. This is contradictory to the sentence right after « At the end of the spectrum are the endoparasites Microsporidia, which have among the smallest known fungal genomes ».

The authors state that pathogens have bigger genomes and then they take an example of a pathogen that has a minimal genome. I know it's probably because they lost genes following the transition to endoparasitism and not related to their capacity to cause disease. I just want to point out that their writing could be more precise. I invite authors to think of young scholars who are new to the field of fungal evolutionary genomics.

We thank the reviewer for prompting us to clarify the text. We rewrote this short extract as follows “Notably, not all pathogenic species experience genome or gene expansions, or show compartmentalized genome architecture. While gene family expansions are important for some pathogens, the contrary can be observed in others, such as Microsporidia. Due to transition to obligatory intracellular lifestyle these fungi show signatures of strong genome contractions and reduced gene repertoire (Katinka et al. 2001) without compromising their ability to induce disease in the host. This raises questions about universal genomic mechanisms of transition to pathogenic state.”

(g) I find it strange that the authors do not cite - and do not present the major results of two other studies that use the same type of approach and ask the same type of question in Sordariomycetes, although not focusing on pathogenicity:

Hensen et al.: https://pubmed.ncbi.nlm.nih.gov/37820761/

Shen et al.: https://pubmed.ncbi.nlm.nih.gov/33148650/

We thank the reviewer for pointing out this omission. We now added more information in the introduction to highlight the importance of the phylogenetic context in studying genome evolution as demonstrated by these studies. The following part was added to introduction:  “Other phylogenomic studies investigating a wide range of Ascomycete species, while not explicitly focusing on the neutral evolution hypothesis, have found strong phylogenetic signals in genome evolution, reflected in distinct genome characteristics (e.g., genome size, gene number, intron number, repeat content) across lineages or families (Shen et al. 2020; Hensen et al. 2023). Variation in genome size has been shown to correlate with the activity of the repeat-induced point mutation (RIP) mechanism (Hensen et al. 2023; Badet and Croll 2025), by which repeated DNA is targeted and mutated. RIP can potentially lead to a slower rate of emergence of new genes via duplication (Galagan et al. 2003), and hinder TE proliferation limiting genome size expansion (Badet and Croll 2025). Variation in genome dynamics across lineages has also been suggested to result from environmental context and lifestyle strategies (Shen et al. 2020), with Saccharomycotina yeast fungi showing reductive genome evolution and Pezizomycotina filamentous fungi exhibiting frequent gene family expansions. Given the strong impact of phylogenetic membership,  demographic history (Ne) and host-specific adaptations of pathogens on their genomes, we reasoned that further examination of genomic sequences in groups of species with various lifestyles can generate predictions regarding the architecture of pathogenic genomes.”

(h) Genome defense mechanisms against repeated elements, such as RIP, are not mentioned while they could have a major impact on genome size (Hensen et al cited above; Badet and Croll https://www.biorxiv.org/content/10.1101/2025.01.10.632494v1.full).

This citation is added in the text above.

(i) Should the reader assume that the genome features to be examined are those mentioned in the first paragraph or those in the penultimate one?

In the last paragraph of the introduction we included the complete list of investigated genomic traits.

(j) The insect-associated lifestyle is mentioned only in the research questions on page 4, but not earlier in the introduction. Why should we care about insect-associated fungi?

We apologize for this omission. We added a sentence explaining how neutral evolution hypotheses can explain patterns of genome evolution in endoparasites and species with specialized vectors (traits present in insect-associated species) and added a sentence in the last paragraph that this is the reason why we have selected this trait for analysis.  

(2) Why use concatenation to infer phylogeny?

(a) Kapli et al. https://pubmed.ncbi.nlm.nih.gov/32424311/ « Analyses of both simulated and empirical data suggest that full likelihood methods are superior to the approximate coalescent methods and to concatenation »

(b) It also seems that a homogeneous model was used, and not a partitioned model, while the latter are more powerful. Why?

We thank the reviewer for the comment. When we were reconstructing the phylogenetic tree  we were not aware of the publication and we followed common practices from literature for phylogenetic tree reconstruction even though currently they are not regarded as most optimal. In fact, in the first round of submission, we have included both concatenation as well as a multispecies coalescent method based on 1000 busco sequences and a concatenation method with different partitions for 250 busco sequences. All three methods produced similar topologies. Since the results were concordant, we chose to omit these analyses from the manuscript to streamline the presentation and focus on the most important results.

(3) Other comments:

Is there a table listing lifestyles?

Yes, lifestyles (pathogenicity and insect-association) are listed in Supplementary Table S1. 

(4) Summary:

(a) seemingly similar pathogens »: meaning unclear; on what basis are they similar? why « seemingly »?

We removed “seemingly” from the sentence.

(b) Page 4: what's the difference between genome feature and genome trait?

There is no difference. We apologize for the confusion. We changed “feature” to “trait” whenever it refers to the specific 13 genomic traits analyzed in this study.

(c) Page 22: Braker, not Breaker

corrected

What do the authors mean when they write that genes were predicted with Augustus and Braker? Do they mean that the two sets of gene models were combined? Gene counts are based on Augustus (P24): why not Braker?

We only meant here that gene annotation was performed using Braker pipeline, which uses a particular version of Augustus. We corrected the sentence.

(d) Figure 2B and 2C:

'Undetermined sign' or 'Positive/Negative' would be better than « YES » or it's just impossible to understand the figure without reading the legend.

We changed “YES” to “UNDETERMINED SIGN” as suggested by the reviewer.

Author response:

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

Reviewer #1(Public Reviews):

Summary: 

Here, Millet et al. consider whether the nematode C. elegans 'discounts' the value of reward due to effort in a manner similar to that shown in other species, including rodents and humans. They designed a T-maze effort choice paradigm inspired by previous literature, but manipulated how effortful the food is to consume.C. elegans worms were sensitive to this novel manipulation, exhibiting effort-discountinglike behaviour that could be shaped by varying the density of food at each alternative in order to calculate an indifference point. This discounting-like behaviour was related to worms' rates of patch leaving, which differed between the low and high effort patches in isolation. The authors also found a potential relationship to dopamine signalling, and also that this discounting behaviour was not specific to lab-based strains of C. elegans . 

Strengths: 

The question is well-motivated, and the approach taken here is novel. The authors are careful in their approach to altering and testing the properties of the effortful, elongated bacteria. Similarly, they go to some effort to understand what exactly is driving behavioural choices in this context, both through the application of simple standard models of effort discounting and a kinetic analysis of patch leaving. The comparisons to various dopamine mutants further extend the translational potential of their findings. I also appreciate the comparison to natural isolate strains, as the question of whether this behaviour may be driven by some sort of strain-specific adaptation to the environment is not regularly addressed in mammalian counterparts. The manuscript is well-written, and the figures are clear and comprehensible. 

Weaknesses: 

Discounting is typically defined as the alteration of a subjective value by effort (or time, risk, etc.), which is then used to guide future decision-making. By adapting the standard t-maze task for C. elegans as a patch-leaving paradigm, the authors observe behaviour strongly consistent with discounting models, but that is likely driven by a different process, in particular by an online estimate of the type of food in the current patch, which then influences patch-leaving dynamics (Figure 3). This is fundamentally different from decision-making strategies relating to effort that have been described in the rodent and human literatures. 

We agree that in our study worms are likely making an on-line estimate of food quality in the current patch, but we wish to point out that rodents and humans also use on-line estimates in some significant effort-discounting paradigms. With respect to rodents, we call attention to effort discounting studies involving the widely used progressive ratio task (references in Discussion). In this task, animals can either lever-press for a preferred food or consume a less preferred food that is freely available nearby. However, the number of lever presses required to obtain preferred food increases as a function of the cumulative number of lever presses until the effort-cost of obtaining preferred food becomes too high and the animal switches to a freely available food. In essence, the lever and the freely available food are patches and the animal decides whether or not to leave the “lever” patch. It seems inescapable that the progressive ratio task involves an on-line assessment of the cost/benefit relationship associated with lever pressing. With respect to humans, one highly cited study (reference in Discussion) presented participants with a series of virtual apple trees. They could see how many apples are in the current tree and how much effort (squeezing a handgrip) is required to gather them. Their task was to decide whether or not to gather apples from that tree based on the perceived cost and benefit. Thus, on-line estimation is a common strategy used by animals and humans as shown in the effort discounting literature. We now make this point in the Discussion section titled A model of effort-discounting like behavior.

Similarly, the calculation of indifference points at the group instead of at the individual level also suggests a different underlying process and limits the translational potential of their findings. The authors do not discuss the implications of these differences or why they chose not to attempt a more analogous trial-based experiment.  

It is not clear to us why changing the read-out –– from the individual level to the population level –– necessarily suggests that a different biological mechanism is at work. In our view, there is one mechanism and it can be seen from different perspectives (e.g., individual vs population). Furthermore, the analogous trial-based experiment, as we understand it, would be to record behavior one worm at a time in the T-maze. This design is not practical because it entails recording a large number of single worms in the T-maze for 60 min each. 

In the case of both the dopamine and natural isolate experiments, the data are very noisy despite large (relative to other C. elegans experiments) sample sizes. In the dopamine experiment, disruption of dop1, dop-2, and cat-2 had no statistically significant effect. There do not appear to be any corrections for multiple comparisons, and the single significant comparison, for dop-3, had a small effect size. 

An ANOVA followed by a Dunnett test was used to test differences between groups in Fig. 4 and 5. The Dunnett test is a multiple comparison test comparing experimental groups to a single control group. It is used to minimize type I error while maintaining statistical power and does not require further correction for multiple comparisons. We have clarified the use of the Dunnett test in the statistical table.  The effect size for dop-3 is 0.5 (Cohen’s d), which is typically interpreted as a medium, not small, effect size.(e.g. Cohen, Psychological Bulletin, 1992, Vol. 112. No. 1,155-159). 

More detailed behavioural analyses on both these and the wild isolate strains, for example by applying their kinetic analysis, would likely give greater insight as to what is driving these inconsistent effects. 

More detailed behavioral analysis could reveal why we observe a difference in effort discounting in some strains and not others. However, it is not obvious what type of behavioral analysis would be needed to differentiate between pleiotropic effects of the mutations/natural isolates and more specific effects on effort discounting. A simple kinetic analysis in particular may not be enough to reveal relevant differences between mutants/natural isolates. For this reason, we think that such experiments may be better suited for future follow up studies.

Reviewer #2 (Public Reviews)

Summary: 

Millet et al. show that C. elegans systematically prefers easy-to-eat bacteria but will switch its choice when harder-to-eat bacteria are offered at higher densities, producing indifference points that fit standard economic discounting models. Detailed kinetic analysis reveals that this bias arises from unchanged patch-entry rates but significantly elevated exit rates on effortful food, and dop-3 mutants lose the preference altogether, implicating dopamine in effort sensitivity. These findings extend effortdiscounting behavior to a simple nematode, pushing the phylogenetic boundary of economic costbenefit decision-making. 

Strengths: 

(1) Extends the well-characterized concept of effort discounting into C. elegans , setting a new phylogenetic boundary and opening invertebrate genetics to economic-behavior studies. 

(2) Elegant use of cephalexin-elongated bacteria to manipulate "effort" without altering nutritional or olfactory cues, yielding clear preference reversals and reproducible indifference points. 

(3) Application of standard discounting models to predict novel indifference points is both rigorous and quantitatively satisfying, reinforcing the interpretation of worm behavior in economic terms. 

(4) The three-state patch-model cleanly separates entry and exit dynamics, showing that increased leaving rates-rather than altered re-entry-drive choice biases. 

(5) Investigates the role of dopamine in this behavior to try to establish shared mechanisms with vertebrates. 

(6) Demonstration of discounting in wild strain (solid evidence). 

Weaknesses: 

(1) The kinetic model omits rich trajectory details-such as turning angles or hazard functions-that could distinguish a bona fide roaming transition from other exit behaviors. 

The overarching goal of present paper was to develop a simple model for effort discounting in a small, genetically tractable organism.  Accordingly,  we focused on quantitative assays that are easy to implement and analyze. The patch-leaving assay and its associated kinetic analysis are one such assay. To keep things simple in this assay, we counted the number of  transitions between the three states shown in Fig. 3A. We chose not to analyze the data in terms of turning angles or hazard functions because the metrics we developed seemed sufficient. Finally, we note that there are new modeling data showing that the presumptive transitions into the roaming state can be explained in terms of a one-state stochastic model in which there is no discrete roaming state (Elife. 2025 Jul 30;14:RP104972. doi:

10.7554/eLife.104972.PMID: 40736321).

(2) Only dop-3 shows an effect, and the statistical validity of this result is questionable. It is not clear if the authors corrected for multiple comparisons, and the effect size is quite small and noisy, given the large number of worms tested. Other mutants do not show effects. Given these two concerns, the role of dopamine in C. elegans effort discounting was unconvincing. 

An ANOVA followed by a Dunnett test was used to test statistical significance in figures 4 and 5 (see above for a discussion of these tests). We believe this approach is rigorous, and the use of these tests is statistically valid. We note that the effect size for this comparison was medium.

(3) With only five wild isolates tested (and variable data quality), it's hard to conclude that effort discounting isn't a lab-strain artifact or how broadly it varies in natural populations. 

The fact that four of the five natural isolates tested display levels of effort discounting similar to N2 (only one natural isolate does not display effort discounting) argues against effort discounting being a laboratory adaption.  We have nevertheless weakened the claim regarding natural isolates. We now say effort discounting-like behavior may not be an adaptation to the laboratory environment.  

(4) Detailed analysis of behavior beyond preference indices would strengthen the dopamine link and the claim of effort discounting in wild strains. 

Going beyond preference in the behavioral analysis might or might not reveal new phenotypes that strengthen the link with dopamine. At present, however, we think such experiments are beyond the scope of the paper.

(5) A few mechanistic statements (e.g., tying satiety exclusively to nutrient signals) would benefit from explicit citations or brief clarifications for non-worm specialists. 

We are unable to identify a mechanistic statement tying satiety to nutrient signals in our manuscript.

Reviewer #3 (Public Reviews)

Summary: 

The authors establish a behavioral task to explore effort discounting in C. eleganss . By using bacterial food that takes longer to consume, the authors show that, for equivalent effort, as measured by pumping rate, they obtain less food, as measured by fat deposition. The authors formalize the task by applying a formal neuroeconomic decision-making model that includes value, effort, and discounting. They use this to estimate the discounting that C. elegans applies based on ingestion effort by using a population-level 2-choice T-maze. They then analyze the behavioral dynamics of individual animals transitioning between on-food and off-food states. Harder to ingest bacteria led to increased food patch leaving. Finally, they examined a set of mutants defective in different aspects of dopamine signaling, as dopamine plays a key role in discounting in vertebrates and regulates certain aspects of C. elegans foraging. 

Strengths: 

The behavioral experiments and neuroeconomic analysis framework are compelling, interesting, and make a significant contribution to the field. While these foraging behaviors have been extensively studied, few include clearly articulated theoretical models to be tested. 

Demonstrating that C. elegans effort discounting fits model predictions and has stable indifference points is important for establishing these tasks as a model for decision making. 

Weaknesses: 

The dopamine experiments are harder to interpret. The authors point out the perplexing lack of an effect of dat-1 and cat-2. dop-3 leads to general indifference. I am not sure this is the expected result if the argument is a parallel functional role to discounting in vertebrates. dop-3 causes a range of locomotor phenotypes and may affect feeding (reduced fat storage), and thus, there may be a general defect in the ability to perform the task rather than anything specific to discounting.

That said, some of the other DA mutants also have locomotor defects and do not differ from N2. But there is no clear result here - my concern is that global mutants in such a critical pathway exhibit such pleiotropy that it's difficult to conclude there is a clear and specific role for DA in effort discounting. This would require more targeted or cell-specific approaches. 

We agree with the reviewer that the results of the dopamine experiments are puzzling and getting a better understanding of the role of dopamine in effort-discounting will require more sensitive assays and different experimental approaches (e.g. cell-specific rescues). However, as mentioned by the reviewer, all the mutations tested have some pleiotropic effects, yet only dop-3 displays a defect in effort discounting. This, in our opinion, points to a specific role of dop-3 in effort-discounting in C. elegans. This point is now made in the Discussion in the section titled Role of dopamine signaling in effort discountinglike behavior.

Meanwhile, there are other pathways known to affect responses to food and patch leaving decisions: serotonin, pigment-dispersing factor, tyramine, etc. The paper would have benefited from a clarification about why these were not considered as promising candidates to test (in addition to or instead of dopamine). 

We focused on DA because of its well-established effect on effort discounting in rodents.

Testing other pathways is a goal for future research.

Reviewer #1 (Recommendations for the authors):

The current results are more a reframing of data gathered from a patch-leaving paradigm, but described in the form of economic choice modelling in which discounting is one possible explanation. One more parsimonious explanation that worms estimate in real-time some rate of reward and leave the patch at some threshold, consistent with canonical foraging models, previous experiments in C. elegans, and the authors' own data (Figure 3). Therefore, I am wary about some of the claims made in this manuscript, such as 'decision-making strategies based on effort-cost trade-offs are evolutionarily conserved'. 

These points are now addressed in the Discussion in a revised section titled A model of effortdiscounting like behavior. (i) We now call attention to the fact that our T-maze assay is a patch-leaving foraging paradigm. (ii) We now propose a revised model in which “worms make an on-line assessment of food value in the current patch which in turn alters patch-leaving dynamics, increasing the exit rates from cephalexin-treated patches as shown in Figure 3.” (iii) We now provide evidence from the rodent and human literature that the strategy of on-line assessment of reward value may be evolutionarily conserved in the case of a class of effort discounting tasks whose solution requires on-line assessments. 

If the reason the authors chose to do a patch-leaving style task rather than a traditional t-maze is because C. elegans is unable to retain the sort of information necessary to make such simultaneous decisions - e.g., if pre-training on the two options isn't possible - then this in itself suggests that mechanisms underlying these decisions in worms and mammals are unlikely to be the same. I mention this because I would like to suggest to the authors an alternative interpretation: that patch foraging is actually 'the' canonical computation that translates across species. This would, in fact, be nicely consistent with some other recent modelling work in humans, e.g., https://www.biorxiv.org/content/10.1101/2025.05.06.652482v1. 

Please see the previous response.

Reviewer #2 (Recommendations for the authors):

Can you provide a picture of the regular and CEPH bacteria? 

Done (see Figure 1––figure supplement 1).

Reviewer #3 (Recommendations for the authors):

I would recommend testing representative mutants in other pathways in the choice task. If possible, more targeted experiments with dop-3, including either cell-specific KOs or rescues, would very much strengthen this aspect of the paper. 

While valuable, these experiments are out of scope for the present study.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Bansal et al. present a study on the fundamental blood and nectar feeding behaviors of the critical disease vector, Anopheles stephensi. The study encompasses not just the fundamental changes in blood feeding behaviors of the crucially understudied vector, but then uses a transcriptomic approach to identify candidate neuromodulation pathways which influence blood feeding behavior in this mosquito species. The authors then provide evidence through RNAi knockdown of candidate pathways that the neuromodulators sNPF and Rya modulate feeding either via their physiological activity in the brain alone or through joint physiological activity along the brain-gut axis (but critically not the gut alone). Overall, I found this study to be built on tractable, well-designed behavioral experiments.

Their study begins with a well-structured experiment to assess how the feeding behaviors of A. stephensi change over the course of its life history and in response to its age, mating, and oviposition status. The authors are careful and validate their experimental paradigm in the more well-studied Ae. aegypti, and are able to recapitulate the results of prior studies, which show that mating is a prerequisite for blood feeding behaviors in Ae. aegypt. Here they find A. Stephensi, like other Anopheline mosquitoes, has a more nuanced regulation of its blood and nectar feeding behaviors.

The authors then go on to show in a Y-maze olfactometer that ,to some degree, changes in blood feeding status depend on behavioral modulation to host cues, and this is not likely to be a simple change to the biting behaviors alone. I was especially struck by the swap in valence of the host cues for the blood-fed and mated individuals, which had not yet oviposited. This indicates that there is a change in behavior that is not simply desensitization to host cues while navigating in flight, but something much more exciting is happening.

The authors then use a transcriptomic approach to identify candidate genes in the blood-feeding stages of the mosquito's life cycle to identify a list of 9 candidates that have a role in regulating the host-seeking status of A. stephensi. Then, through investigations of gene knockdown of candidates, they identify the dual action of RYa and sNPF and candidate neuromodulators of host-seeking in this species. Overall, I found the experiments to be well-designed. I found the molecular approach to be sound. While I do not think the molecular approach is necessarily an all-encompassing mechanism identification (owing mostly to the fact that genetic resources are not yet available in A. stephensi as they are in other dipteran models), I think it sets up a rich line of research questions for the neurobiology of mosquito behavioral plasticity and comparative evolution of neuromodulator action.

We appreciate the reviewer’s detailed summary of our work. We thank them for their positive comments and agree with them on the shortcomings of our approach.

Strengths:

I am especially impressed by the authors' attention to small details in the course of this article. As I read and evaluated this article, I continued to think about how many crucial details could potentially have been missed if this had not been the approach. The attention to detail paid off in spades and allowed the authors to carefully tease apart molecular candidates of blood-seeking stages. The authors' top-down approach to identifying RYamide and sNPF starting from first principles behavioral experiments is especially comprehensive. The results from both the behavioral and molecular target studies will have broad implications for the vectorial capacity of this species and comparative evolution of neural circuit modulation.

We really appreciate that the reviewer has recognised the attention to detail we have tried to put, thank you!

Weaknesses:

There are a few elements of data visualizations and methodological reporting that I found confusing on a first few read-throughs. Figure 1F, for example, was initially confusing as it made it seem as though there were multiple 2-choice assays for each of the conditions. I would recommend removing the "X" marker from the x-axis to indicate the mosquitoes did not feed from either nectar, blood, or neither in order to make it clear that there was one assay in which mosquitoes had access to both food sources, and the data quantify if they took both meals, one meal, or no meals.

We thank the reviewer for flagging the schematic in figure 1F. As suggested, we have removed the “X” markers from the x-axis and revised the axis label from “choice of food” to “choice made” to better reflect what food the mosquitoes chose in the assay. For clarity, we have now also plotted the same data as stacked graphs at the bottom of Fig. 1F, which clearly shows the proportion of mosquitoes fed on each particular choice. We avoid the stacked graph as the sole representation of this data, as it does not capture the variability in the data.

I would also like to know more about how the authors achieved tissue-specific knockdown for RNAi experiments. I think this is an intriguing methodology, but I could not figure out from the methods why injections either had whole-body or abdomen-specific knockdown.

The tissue-specific knockdown (abdomen only or abdomen+head) emerged from initial standardisations where we were unable to achieve knockdown in the head unless we used higher concentrations of dsRNA and did the injections in older females. We realised that this gave us the opportunity to isolate the neuronal contribution of these neuropeptides in the phenotype produced. Further optimisations revealed that injecting dsRNA into 0-10h old females produced abdomen-specific knockdowns without affecting head expression, whereas injections into 4 days old females resulted in knockdowns in both tissues. Moreover, head knockdowns in older females required higher dsRNA concentrations, with knockdown efficiency correlating with the amount injected. In contrast, abdominal knockdowns in younger females could be achieved even with lower dsRNA amounts.

We have mentioned the knockdown conditions- time of injection and the amount dsRNA injected- for tissue-specific knockdowns in methods but realise now that it does not explain this well enough. We have now edited it to state our methodology more clearly (see lines 932-948).

I also found some interpretations of the transcriptomic to be overly broad for what transcriptomes can actually tell us about the organism's state. For example, the authors mention, "Interestingly, we found that  after a blood meal, glucose is neither spent nor stored, and that the female brain goes into a state of metabolic 'sugar rest', while actively processing proteins (Figure S2B, S3)".

This would require a physiological measurement to actually know. It certainly suggests that there are changes in carbohydrate metabolism, but there are too many alternative interpretations to make this broad claim from transcriptomic data alone.

We thank the reviewer for pointing this out and agree with them. We have now edited our statement to read:

“Instead, our data suggests altered carbohydrate metabolism  after a blood meal, with the female brain potentially entering a state of metabolic 'sugar rest' while actively processing proteins (Figure S2B, S3). However, physiological measurements of carbohydrate and protein metabolism will be required to confirm whether glucose is indeed neither spent nor stored during this period.” See lines 271-277.

Reviewer #2 (Public review):

Summary:

In this manuscript, Bansal et al examine and characterize feeding behaviour in Anopheles stephensi mosquitoes. While sharing some similarities to the well-studied Aedes aegypti mosquito, the authors demonstrate that mated females, but not unmated (virgin) females, exhibit suppression in their bloodfeeding behaviour. Using brain transcriptomic analysis comparing sugar-fed, blood-fed, and starved mosquitoes, several candidate genes potentially responsible for influencing blood-feeding behaviour were identified, including two neuropeptides (short NPF and RYamide) that are known to modulate feeding behaviour in other mosquito species. Using molecular tools, including in situ hybridization, the authors map the distribution of cells producing these neuropeptides in the nervous system and in the gut. Further, by implementing systemic RNA interference (RNAi), the study suggests that both neuropeptides appear to promote blood-feeding (but do not impact sugar feeding), although the impact was observed only  after both neuropeptide genes underwent knockdown.

Strengths and/or weaknesses:

Overall, the manuscript was well-written; however, the authors should review carefully, as some sections would benefit from restructuring to improve clarity. Some statements need to be rectified as they are factually inaccurate.

Below are specific concerns and clarifications needed in the opinion of this reviewer:

(1) What does "central brains" refer to in abstract and in other sections of the manuscript (including methods and results)? This term is ambiguous, and the authors should more clearly define what specific components of the central nervous system was/were used in their study.

Central brain, or mid brain, is a commonly used term to refer to brain structures/neuropils without the optic lobes (For example: https://www.nature.com/articles/s41586-024-07686-5). In this study we have focused our analysis on the central brain circuits involved in modulating blood-feeding behaviour and have therefore excluded the optic lobes. As optic lobes account for nearly half of all the neurons in the mosquito brain (https://pmc.ncbi.nlm.nih.gov/articles/PMC8121336/), including them would have disproportionately skewed our transcriptomic data toward visual processing pathways.

We have indicated this in figure 3A and in the methods (see lines 800-801, 812). We have now also clarified it in the results section for neuro-transcriptomics to avoid confusion (see lines 236-237).

(2) The abstract states that two neuropeptides, sNPF and RYamide are working together, but no evidence is summarized for the latter in this section.

We thank the reviewer for pointing this out. We have now added a statement “This occurs in the context of the action of RYa in the brain” to end of the abstract, for a complete summary of our proposed model.

(3) Figure 1

Panel A: This should include mating events in the reproductive cycle to demonstrate differences in the feeding behavior of Ae. aegypti.

Our data suggest that mating can occur at any time between eclosion and oviposition in An. stephensi and between eclosion and blood feeding in Ae. aegypti. Adding these into (already busy) 1A, would cloud the purpose of the schematic, which is to indicate the time points used in the behavioural assays and transcriptomics.

Panel F: In treatments where insects were not provided either blood or sugar, how is it that some females and males had fed? Also, it is unclear why the y-axis label is % fed when the caption indicates this is a choice assay. Also, it is interesting that sugar-starved females did not increase sugar intake. Is there any explanation for this (was it expected)?

We apologise for the confusion. The experiment is indeed a choice assay in which sugar-starved or sugar-sated females, co-housed with males, were provided simultaneous access to both blood and sugar, and were assessed for the choice made (indicated on the x-axis): both blood and sugar, blood only, sugar only, or neither. The x-axis indicates the choice made by the mosquitoes, not the choice provided in the assay, and the y-axis indicates the percentage of males or females that made each particular choice. We have now removed the “X” markers from the x-axis and revised the axis label from “choice of food” to “choice made” to better reflect what food the mosquitoes chose to take.

In this assay, we scored females only for the presence or absence of each meal type (blood or sugar) and are therefore unable to comment on whether sugar-starved females consumed more sugar than sugarsated females. However, when sugar-starved, a higher proportion of females consumed both blood and sugar, while fewer fed on blood alone.

For clarity, we have now also plotted the same data as stacked graphs at the bottom of Fig. 1F, which clearly shows the proportion of mosquitoes fed on each particular choice. We avoid the stacked graph as the sole representation of this data as it does not capture the variability in the data.

(4) Figure 3

In the neurotranscriptome analysis of the (central) brain involving the two types of comparisons, can the authors clarify what "excluded in males" refers to? Does this imply that only genes not expressed in males were considered in the analysis? If so, what about co-expressed genes that have a specific function in female feeding behaviour?

This is indeed correct. We reasoned that since blood feeding is exclusive to females, we should focus our analysis on genes that were specifically upregulated in them. As the reviewer points out, it is very likely that genes commonly upregulated in males and females may also promote blood feeding and we will miss out on any such candidates based on our selection criteria.

(5) Figure 4

The authors state that there is more efficient knockdown in the head of unfed females; however, this is not accurate since they only get knockdown in unfed animals, and no evidence of any knockdown in fed animals (panel D). This point should be revised in the results test as well.

Perhaps we do not understand the reviewer’s point or there has been a misunderstanding. In figure 4D, we show that while there is more robust gene knockdown in unfed females, blood-fed females also showed modest but measurable knockdowns ranging from 5-40% for RYamide and 2-21% for sNPF.

Relatedly, blood-feeding is decreased when both neuropeptide transcripts are targeted compared to uninjected (panel C) but not compared to dsGFP injected (panel E). Why is this the case if authors showed earlier in this figure (panel B) that dsGFP does not impact blood feeding?

We realise this concern stems from our representation of the data. Since we had earlier determined that dsGFP-injected females fed similarly to uninjected females (fig 4B), we used these controls interchangeably in subsequent experiments. To avoid confusion, we have now only used the label ‘control’ in figure 4 (and supplementary figure S9) and specified which control was used for each experiment in the legend.

In addition to this, we wanted to clarify that fig 4C and 4E are independent experiments. 4C is the behaviour corresponding to when the neuropeptides were knocked down in both heads and abdomens.

4E is the behaviour corresponding to when the neuropeptides were knocked down in only the abdomens. We have now added a schematic in the plots to make this clearer.

In addition, do the uninjected and dsGFP-injected relative mRNA expression data reflect combined RYa and sNPF levels? Why is there no variation in these data,…

In these qPCRs, we calculated relative mRNA expression using the delta-delta Ct method (see line 975). For each neuropeptide its respective control was used. For simplicity, we combined the RYa and sNPF control data into a single representation. The value of this control is invariant because this method sets the control baseline to a value of 1.

…and how do transcript levels of RYa and sNPF compare in the brain versus the abdomen (the presentation of data doesn't make this relationship clear).

The reviewer is correct in pointing out that we have not clarified this relationship in our current presentation. While we have not performed absolute mRNA quantifications, we extracted relative mRNA levels from qPCR data of 96h old unmanipulated control females. We observed that both sNPF and RYa transcripts are expressed at much lower levels in the abdomens, as compared to those in the heads, as shown in the graphs inserted below.

Author response image 1.

(6) As an overall comment, the figure captions are far too long and include redundant text presented in the methods and results sections.

We thank the reviewer for flagging this and have now edited the legends to remove redundancy.

(7) Criteria used for identifying neuropeptides promoting blood-feeding: statement that reads "all neuropeptides, since these are known to regulate feeding behaviours". This is not accurate since not all neuropeptides govern feeding behaviors, while certainly a subset do play a role.

We agree with the reviewer that not all neuropeptides regulate feeding behaviours. Our statement refers to the screening approach we used: in our shortlist of candidates, we chose to validate all neuropeptides.

(8) In the section beginning with "Two neuropeptides - sNPF and RYa - showed about 25% and 40% reduced mRNA levels...", the authors state that there was no change in blood-feeding and later state the opposite. The wording should be clarified as it is unclear.

Thank you for pointing this out. We were referring to an unchanged proportion of the blood fed females. We have now edited the text to the following:

“Two neuropeptides - sNPF and RYa - showed about 25% and 40% reduced mRNA levels in the heads but the proportion of females that took blood meals remained unchanged”. See lines 338-340.

(9) Just before the conclusions section, the statement that "neuropeptide receptors are often ligand promiscuous" is unjustified. Indeed, many studies have shown in heterologous systems that high concentrations of structurally related peptides, which are not physiologically relevant, might cross-react and activate a receptor belonging to a different peptide family; however, the natural ligand is often many times more potent (in most cases, orders of magnitude) than structurally related peptides. This is certainly the case for various RYamide and sNPF receptors characterized in various insect species.

We agree with the reviewer and apologise for the mistake. We have now removed the statement.

(10) Methods

In the dsRNA-mediated gene knockdown section, the authors could more clearly describe how much dsRNA was injected per target. At the moment, the reader must carry out calculations based on the concentrations provided and the injected volume range provided later in this section.

We have now edited the section to reflect the amount of dsRNA injected per target. Please see lines 921-931.

It is also unclear how tissue-specific knockdown was achieved by performing injection on different days/times. The authors need to explain/support, and justify how temporal differences in injection lead to changes in tissue-specific expression. Does the blood-brain barrier limit knockdown in the brain instead, while leaving expression in the peripheral organs susceptible?

To achieve tissue-specific knockdowns of sNPF and RYa, we optimised both the time of injection as well as the dsRNA concentration to be injected. Injecting dsRNA into 0-10h females produced abdomen specific knockdowns without affecting head expression, whereas injections into 96h old females resulted in knockdowns in both tissues. Head knockdowns in older females required higher dsRNA concentrations, with knockdown efficiency correlating with the amount injected. In contrast, abdominal knockdowns in younger females could be achieved even with lower dsRNA amounts, reflecting the lower baseline expression of sNPF in abdomens compared to heads and the age-dependent increase in head expression (as confirmed by qPCR). It is possible that the blood-brain barrier also limits the dsRNA entering the brain, thereby requiring higher amounts to be injected for head knockdowns.

We have now edited this section to state our methodology more clearly (see lines 932-948).

For example, in Figure 4, the data support that knockdown in the head/brain is only effective in unfed animals compared to uninjected animals, while there is no evidence of knockdown in the brain relative to dsGFP-injected animals. Comparatively, evidence appears to show stronger evidence of abdominal knockdown mostly for the RYa transcript (>90%) while still significantly for the sNPF transcript (>60%).

As we explained earlier, this concern likely stems from our representation of the data. Since we had earlier determined that dsGFP-injected females fed similarly to uninjected females (fig 4B), we used these controls interchangeably in subsequent experiments. To avoid confusion, we have now only used the label ‘control’ in figure 4 (and supplementary figure S9) and specified which control was used for each experiment in the legend.

In addition to this, we wanted to clarify that fig 4C and 4E are independent experiments. 4C is the behaviour corresponding to when the neuropeptides were knocked down in both heads and abdomens. 4E is the behaviour corresponding to when the neuropeptides were knocked down in only the abdomen. We have now added a schematic in the plots to make this clearer.

Reviewer #3 (Public review):

Summary:

This manuscript investigates the regulation of host-seeking behavior in Anopheles stephensi females across different life stages and mating states. Through transcriptomic profiling, the authors identify differential gene expression between "blood-hungry" and "blood-sated" states. Two neuropeptides, sNPF and RYamide, are highlighted as potential mediators of host-seeking behavior. RNAi knockdown of these peptides alters host-seeking activity, and their expression is anatomically mapped in the mosquito brain (sNPF and RYamide) and midgut (sNPF only).

Strengths:

(1) The study addresses an important question in mosquito biology, with relevance to vector control and disease transmission.

(2) Transcriptomic profiling is used to uncover gene expression changes linked to behavioral states.

(3) The identification of sNPF and RYamide as candidate regulators provides a clear focus for downstream mechanistic work.

(3) RNAi experiments demonstrate that these neuropeptides are necessary for normal host-seeking behavior.

(4) Anatomical localization of neuropeptide expression adds depth to the functional findings.

Weaknesses:

(1) The title implies that the neuropeptides promote host-seeking, but sufficiency is not demonstrated (for example, with peptide injection or overexpression experiments).

Demonstrating sufficiency would require injecting sNPF peptide or its agonist. To date, no small-molecule agonists (or antagonists) that selectively mimic sNPF or RYa neuropeptides have been identified in insects. An NPY analogue, TM30335, has been reported to activate the Aedes aegypti NPY-like receptor 7 (NPYLR7; Duvall et al., 2019), which is also activated by sNPF peptides at higher doses (Liesch et al., 2013). Unfortunately, the compound is no longer available because its manufacturer, 7TM Pharma, has ceased operations. Synthesising the peptides is a possibility that we will explore in the future.

(2) The proposed model regarding central versus peripheral (gut) peptide action is inconsistently presented and lacks strong experimental support.

The best way to address this would be to conduct tissue-specific manipulations, the tools for which are not available in this species. Our approach to achieve head+abdomen and abdomen only knockdown was the closest we could get to achieving tissue specificity and allowed us to confirm that knockdown in the head was necessary for the phenotype. However, as the reviewer points out, this did not allow us to rule out any involvement of the abdomen. This point has been addressed in lines 364-371.

(3) Some conclusions appear premature based on the current data and would benefit from additional functional validation.

The most definitive way of demonstrating necessity of sNPF and RYa in blood feeding would be to generate mutant lines. While we are pursuing this line of experiments, they lie beyond the scope of a revision. In its absence, we relied on the knockdown of the genes using dsRNA. We would like to posit that despite only partial knockdown, mosquitoes do display defects in blood-feeding behaviour, without affecting sugar-feeding. We think this reflects the importance of sNPF in promoting blood feeding.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Overall, I found this manuscript to be well-prepared, visually the figures are great and clearly were carefully thought out and curated, and the research is impacwul. It was a wonderful read from start to finish. I have the following recommendations:

Thank you very much, we are very pleased to hear that you enjoyed reading our manuscript!

(1) For future manuscripts, it would make things significantly easier on the reviewer side to submit a format that uses line numbers.

We sincerely apologise for the oversight. We have now incorporated line numbers in the revised manuscript.

(2) There are a few statements in the text that I think may need clarification or might be outside the bounds of what was actually studied here. For example, in the introduction "However, mating is dispensable in Anophelines even under conditions of nutritional satiety". I am uncertain what is meant by this statement - please clarify.

We apologise for the lack of clarity in the statement and have now deleted it since we felt it was not necessary.

(3) Typo/Grammatical minutiae:

a) A small idiosyncrasy of using hyphens in compound words should also be fixed throughout. Typically, you don't hyphenate if the words are being used as a noun, as in the case: e.g. "Age affects blood feeding.". However, you would hyphenate if the two words are used as a compound adjective "Age affects blood-feeding behavior". This may not be an all-inclusive list, but here are some examples where hyphens need to either be removed or added. Some examples:

"Nutritional state also influences other internal state outputs on blood-feeding": blood-feeding -> blood feeding

"... the modulation of blood-feeding": blood-feeding -> blood feeding

"For example, whether virgin females take blood-meals...": blood-meals -> blood meals

".... how internal and external cues shape meal-choice"-> meal choice

"blood-meal" is often used throughout the text, but is correctly "blood meal" in the figures.

There are many more examples throughout.

We apologise for these errors and appreciate the reviewer’s keen eye. We have now fixed them throughout the manuscript.

b) Figure 1 Caption has a typo: "co-housed males were accessed for sugar-feeding" should be "co-housed males were assessed for sugar feeding"

We apologise for the typo and thank the reviewer for spotting it. We have now corrected this.

c) It would be helpful in some other figure captions to more clearly label which statement is relevant to which part of the text. For example, in Figure 4's caption.

"C,D. Blood-feeding and sugar-feeding behaviour of females when both RYa and sNPF are knocked down in the head (C). Relative mRNA expressions of RYa and sNPF in the heads of dsRYa+dssNPF - injected blood-fed and unfed females, as compared to that in uninjected females, analysed via qPCR (D)."

I found re-referencing C and D at the end of their statements makes it look as thought C precedes the "Relative mRNA expression" and on a first read through, I thought the figure captions were backwards. I'd recommend reformating here and throughout consistently to only have the figure letter precede its relevant caption information, e.g.:

"C. Blood-feeding and sugar-feeding behaviour of females when both RYa and sNPF are knocked down in the head. D. Relative mRNA expressions of RYa and sNPF in the heads of dsRYa+dssNPF - injected bloodfed and unfed females, as compared to that in uninjected females, analysed via qPCR."

We have now edited the legends as suggested.

Reviewer #2 (Recommendations for the authors):

Separately from the clarifications and limitations listed above, the authors could strengthen their study and the conclusions drawn if they could rescue the behavioural phenotype observed following knockdown of sNPF and RYamide. This could be achieved by injection of either sNPF or RYa peptide independently or combined following knockdown to validate the role of these peptides in promoting blood-feeding in An. stephensi. Additionally, the apparent (but unclear) regionalized (or tissue-specific) knockdown of sNPF and RYamide transcripts could be visualized and verified by implementing HCR in situ hyb in knockdown animals (or immunohistochemistry using antibodies specific for these two neuropeptides).

In a follow up of this work, we are generating mutants and peptides for these candidates and are planning to conduct exactly the experiments the reviewer suggests.

Reviewer #3 (Recommendations for the authors):

The loss-of-function data suggest necessity but not sufficiency. Synthetic peptide injection in non-host seeking (blood-fed mated or juvenile) mosquitoes would provide direct evidence for peptide-induced behavioral activation. The lack of these experiments weakens the central claim of the paper that these neuropeptides directly promote blood feeding.

As noted above, we plan to synthesise the peptide to test rescue in a mutant background and sufficiency.

Some of the claims about knockdown efficiency and interpretation are conflicting; the authors dismiss Hairy and Prp as candidates due to 30-35% knockdown, yet base major conclusions on sNPF and RYamide knockdowns with comparable efficiencies (25-40%). This inconsistency should be addressed, or the justification for different thresholds should be clearly stated.

We have not defined any specific knockdown efficacy thresholds in the manuscript, as these can vary considerably between genes, and in some cases, even modest reductions can be sufficient to produce detectable phenotypes. For example, knockdown efficiencies of even as low as about 25% - 40% gave us observable phenotypes for sNPF and RYa RNAi (Figure S9B-G).

No such phenotypes were observed for Hairy (30%) or Prp (35%) knockdowns. Either these genes are not involved in blood feeding, or the knockdown was not sufficient for these specific genes to induce phenotypes. We cannot distinguish between these scenarios.

The observation that knockdown animals take smaller blood meals is interesting and could reflect a downstream effect of altered host-seeking or an independent physiological change. The relationship between meal size and host-seeking behavior should be clarified.

We agree with the reviewer that the reduced meal size observed in sNPF and RYa knockdown animals could result from their inability to seek a host or due to an independent effect on blood meal intake. Unfortunately, we did not measure host-seeking in these animals. We plan to distinguish between these possibilities using mutants in future work.

Several figures are difficult to interpret due to cluttered labeling and poorly distinguishable color schemes. Simplifying these and improving contrast (especially for co-housed vs. virgin conditions) would enhance readability.

We regret that the reviewer found the figures difficult to follow. We have now revised our annotations throughout the manuscript for enhanced readability. For example, “D1^B” is now “D1^PBM” (post-bloodmeal) and “D1^O” is now “D1^PO” (post-oviposition). Wherever mated females were used, we have now appended “(m)” to the annotations and consistently depicted these females with striped abdomens in all the schematics. We believe these changes will improve clarity and readability.

The manuscript does not clearly justify the use of whole-brain RNA sequencing to identify peptides involved in metabolic or peripheral processes. Given that anticipatory feeding signals are often peripheral, the logic for brain transcriptomics should be explained.

The reviewer is correct in pointing out that feeding signals could also emerge from peripheral tissues. Signals from these tissues – in response to both changing nutritional and reproductive states – are then integrated by the central brain to modulate feeding choices. For example, in Drosophila, increased protein intake is mediated by central brain circuitry including those in the SEZ and central complex (Munch et al., 2022; Liu et al., 2017; Goldschmidt et al., 2023). In the context of mating, male-derived sex peptide further increases protein feeding by acting on a dedicated central brain circuitry (Walker et al., 2015). We, therefore focused on the central brain for our studies.

The proposed model suggests brain-derived peptides initiate feeding, while gut peptides provide feedback. However, gut-specific knockdowns had no effect, undermining this hypothesis. Conversely, the authors also suggest abdominal involvement based on RNAi results. These contradictions need to be resolved into a consistent model.

We thank the reviewer for raising this point and recognise their concern. Our reasons for invoking an involvement of the gut were two-fold:

(1) We find increased sNPF transcript expression in the entero-endocrine cells of the midgut in blood-hungry females, which returns to baseline  after a blood-meal (Fig. 4L, M).

(2) While the abdomen-only knockdowns did not affect blood feeding, every effective head knockdown that affected blood feeding also abolished abdominal transcript levels (Fig. S9C, F). (Achieving a head-only reduction proved impossible because (i) systemic dsRNA delivery inevitably reaches the abdomen and (ii) abdominal expression of both peptides is low, leaving little dynamic range for selective manipulation.) Consequently, we can only conclude the following: 1) that brain expression is required for the behaviour, 2) that we cannot exclude a contributory role for gut-derived sNPF. We have discussed this in lines 364-371.

The identification of candidate receptors is promising, but the manuscript would be significantly strengthened by testing whether receptor knockdowns phenocopy peptide knockdowns. Without this, it is difficult to conclude that the identified receptors mediate the behavioral effects.

We agree that functional validation of the receptors would strengthen the evidence for sNPF and RYa_mediated control of blood feeding in _An. stephensi. We selected these receptors based on sequence homology. A possibility remains that sNPF neuropeptides activate more than one receptor, each modulating a distinct circuit, as shown in the case of Drosophila Tachykinin (https://pmc.ncbi.nlm.nih.gov/articles/PMC10184743/). This will mean a systematic characterisation and knockdown of each of them to confirm their role. We are planning these experiments in the future.

The authors compared the percentage changes in sugar-fed and blood-fed animals under sugar-sated or sugar-starved conditions. Figure 1F should reflect what was discussed in the results.

Perhaps this concern stems from our representation of the data in figure 1F? We have now edited the xaxis and revised its label from “choice of food” to “choice made” to better reflect what food the mosquitoes chose to take.

For clarity, we have now also plotted the same data as stacked graphs at the bottom of Fig. 1F, which clearly shows the proportion of mosquitoes fed on each particular choice. We avoid the stacked graph as the sole representation of this data because it does not capture the variability in the data.

Minor issues:

(1) The authors used mosquitoes with belly stripes to indicate mated females. To be consistent, the post-oviposition females should also have belly stripes.

We thank the reviewer for pointing this out. We have now edited all the figures as suggested.

(2) In the first paragraph on the right column of the second page, the authors state, "Since females took blood-meals regardless of their prior sugar-feeding status and only sugar-feeding was selectively suppressed by prior sugar access." Just because the well-fed animals ate less than the starved animals does not mean their feeding behavior was suppressed.

Perhaps there has been a misunderstanding in the experimental setup of figure 1F, probably stemming from our data representation. The experiment is a choice assay in which sugar-starved or sugar-sated females, co-housed with males, were provided simultaneous access to both blood and sugar, and were assessed for the choice made (indicated on the x-axis): both blood and sugar, blood only, sugar only, or neither. We scored females only for the presence or absence of each meal type (blood or sugar) and did not quantify the amount consumed.

(3) The figure legend for Figure 1A and the naming convention for different experimental groups are difficult to follow. A simplified or consistently abbreviated scheme would help readers navigate the figures and text.

We regret that the reviewer found the figure difficult to follow. We have now revised our annotations throughout the manuscript for enhanced readability. For example, “D1^B” is now “D1^PBM” (post-bloodmeal) and “D1^O” is now “D1^PO” (post-oviposition).

(4) In the last paragraph of the Y-maze olfactory assay for host-seeking behaviour in An. stephensi in Methods, the authors state, "When testing blood-fed females, aged-matched sugar-fed females (bloodhungry) were included as positive controls where ever possible, with satisfactory results." The authors should explicitly describe what the criteria are for "satisfactory results".

We apologise for the lack of clarity. We have now edited the statement to read:

“When testing blood-fed females, age-matched sugar-fed females (blood-hungry) were included wherever possible as positive controls. These females consistently showed attraction to host cues, as expected.” See lines 786-790.

(5) In the first paragraph of the dsRNA-mediated gene knockdown section in Methods, dsRNA against GFP is used as a negative control for the injection itself, but not for the potential off-target effect.

We agree with the reviewer that dsGFP injections act as controls only for injection-related behavioural changes, and not for off-target effects of RNAi. We have now corrected the statement. See lines 919-920.

To control for off-target effects, we could have designed multiple dsRNAs targeting different parts of a given gene. We regret not including these controls for potential off-target effects of dsRNAs injected.

(6) References numbers 48, 89, and 90 are not complete citations.

We thank the reviewer for spotting these. We have now corrected these citations.

Author Response:

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

Reviewer #1 (Public review):

The scale bar for fly and ovary images should be included in Figures 9, 10, and 12.

We agree with this comment and apologize for the oversight. We have now modified Figures 9, 10, and 12 to include the scale bars for the ovary images. The fly images were acquired using a stereo microscope where scale bar calculation was not possible. However, all images were acquired at the same magnification for consistency.

Reviewer #2 (Public review):

A weakness of this paper is the phylogenetic analysis to investigate if there is correspondence in the phylogenetic distribution of ITP-type and Gyc76C-type genes/proteins. Unfortunately, the evidence presented is rather limited in scope. Essentially, the authors report that they only found ITP-type and Gyc76C-type genes/proteins in protostomes, but not in deuterostomes. What is needed is a more fine-grained analysis at the species level within the protostomes. However, I recognise that such a detailed analysis may extend beyond the scope of this paper, which is already rich in data.

We thank the reviewer for their comment and the suggestion to perform a fine-grained species level comparison of ITP and Gyc76C genes across protostomes. We are unsure of the utility of this analysis for the present study given that we have now shown that ITPa can activate Gyc76C using both an ex vivo and a heterologous assay, the latter being the gold standard in GPCR and guanylate cyclase discovery (see Huang et al 2025 https://doi.org/10.1073/pnas.2420966122; Beets et al 2023 https://doi.org/10.1016/j.celrep.2023.113058); Chang et al 2009 https://doi.org/10.1073/pnas.0812593106.

Additionally, absence of a gene in a genome/proteome is hard to prove especially when many/most of the protostomian datasets are not as high-quality as those of model systems (e.g. Drosophila melanogaster and Caenorhabditis elegans). Secondly, based on previous findings in Bombyx mori (Nagai et al. 2014 https://doi.org/10.1074/jbc.m114.590646 and Nagai et al. 2016 https://doi.org/10.1371/journal.pone.0156501) and Drosophila (Xu et al. 2023 https://doi.org/10.1038/s41586-023-06833-8 and our study) it is evident that different products of the ITP gene (ITPa and ITPL) could signal via different receptor types depending on the species. Hence, we would need to explore the presence of several genes (ITP, tachykinin, pyrokinin, tachykinin receptor, pyrokinin receptor, CG30340 orphan receptor and Gyc76C) to fully understand which components of these diverse signaling systems are present in a given species to decipher the potential for cross-talk.

While this species-level comparison will certainly be useful in the context of ITP-Gyc76C evolution, it will not alter the conclusions of the present study – ITPa acts via Gyc76C in Drosophila. We therefore agree with the reviewer that these analyses are beyond the scope of this paper.

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

Reviewer #1 (Public Review):  

Summary:  

In Drosophila melanogaster, ITP has functions on feeding, drinking, metabolism, excretion, and circadian rhythm. In the current study, the authors characterized and compared the expression of all three ITP isoforms (ITPa and ITPL1&2) in the CNS and peripheral tissues of Drosophila. An important finding is that they functionally characterized and identified Gyc76C as an ITPa receptor in Drosophila using both in vitro and in vivo approaches. In vitro, the authors nicely confirmed that the inhibitory function of recombinant Drosophila ITPa on MT secretion is Gyc76C-dependent (knockdown Gyc76C specifically in two types of cells abolished the anti-diuretic action of Drosophila ITPa on renal tubules). They also used a combination of multiple approaches to investigate the roles of ITPa and Gyc76C on osmotic and metabolic homeostasis modulation in vivo. They revealed that ITPa signaling to renal tubules and fat body modulates osmotic and metabolic homeostasis via Gyc76C.  

Furthermore, they tried to identify the upstream and downstream of ITP neurons in the nervous system by using connectomics and single-cell transcriptomic analysis. I found this interesting manuscript to be well-written and described. The findings in this study are valuable to help understand how ITP signals work on systemic homeostasis regulation. Both anatomical and single-cell transcriptome analysis here should be useful to many in the field. 

We thank this reviewer for the positive and thorough assessment of our manuscript.  

Strengths:  

The question (what receptors of ITPa in Drosophila) that this study tries to address is important. The authors ruled out the Bombyx ITPa receptor orthologs as potential candidates. They identified a novel ITP receptor by using phylogenetic, anatomical analysis, and both in vitro and in vivo approaches. 

The authors exhibited detailed anatomical data of both ITP isoforms and Gyc76C (in the main and supplementary figures), which helped audiences understand the expression of the neurons studied in the manuscript.  

They also performed connectomes and single-cell transcriptomics analysis to study the synaptic and peptidergic connectivity of ITP-expressing neurons. This provided more information for better understanding and further study on systemic homeostasis modulation.  

Weaknesses:  

In the discussion section, the authors raised the limitations of the current study, which I mostly agree with, such as the lack of verification of direct binding between ITPa and Gyc76C, even though they provided different data to support that ITPa-Gyc76C signaling pathway regulates systemic homeostasis in adult flies. 

We now provide evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Reviewer #2 (Public Review):  

Summary:  

The physiology and behaviour of animals are regulated by a huge variety of neuropeptide signalling systems. In this paper, the authors focus on the neuropeptide ion transport peptide (ITP), which was first identified and named on account of its effects on the locust hindgut (Audsley et al. 1992). Using Drosophila as an experimental model, the authors have mapped the expression of three different isoforms of ITP (Figures 1, S1, and S2), all of which are encoded by the same gene.  

The authors then investigated candidate receptors for isoforms of ITP. Firstly, Drosophila orthologs of G-protein coupled receptors (GPCRs) that have been reported to act as receptors for ITPa or ITPL in the insect Bombyx mori were investigated. Importantly, the authors report that ITPa does not act as a ligand for the GPCRs TkR99D and PK2-R1 (Figure S3). Therefore, the authors investigated other putative receptors for ITPs. Informed by a previously reported finding that ITP-type peptides cause an increase in cGMP levels in cells/tissues (Dircksen, 2009, Nagai et al., 2014), the authors investigated guanylyl cyclases as candidate receptors for ITPs. In particular, the authors suggest that Gyc76C may act as an ITP receptor in Drosophila.  

Evidence that Gyc76C may be involved in mediating effects of ITP in Bombyx was first reported by Nagai et al. (2014) and here the authors present further evidence, based on a proposed concordance in the phylogenetic distribution ITP-type neuropeptides and Gyc76C (Figure 2). Having performed detailed mapping of the expression of Gyc76C in Drosophila (Figures 3, S4, S5, S6), the authors then investigated if Gyc76C knockdown affects the bioactivity of ITPa in Drosophila. The inhibitory effect of ITPa on leucokinin- and diuretic hormone-31-stimulated fluid secretion from Malpighian tubules was found to be abolished when expression of Gyc76C was knocked down in stellate cells and principal cells, respectively (Figure 4). However, as discussed below, this does not provide proof that Gyc76C directly mediates the effect of ITPa by acting as its receptor. The effect of Gyc76C knockdown on the action of ITPa could be an indirect consequence of an alteration in cGMP signalling.  

Having investigated the proposed mechanism of ITPa in Drosophila, the authors then investigated its physiological roles at a systemic level. In Figure 5 the authors present evidence that ITPa is released during desiccation and accordingly, overexpression of ITPa increases survival when animals are subjected to desiccation. Furthermore, knockdown of Gyc76C in stellate or principal cells of Malphigian tubules decreases survival when animals are subject to desiccation. However, whilst this is correlative, it does not prove that Gyc76C mediates the effects of ITPa. The authors investigated the effects of knockdown of Gyc76C in stellate or principal cells of Malphigian tubules on i). survival when animals are subject to salt stress and ii). time taken to recover from of chill coma. It is not clear, however, why animals overexpressing ITPa were also not tested for its effect on i). survival when animals are subject to salt stress and ii). time taken to recover from of chill coma. In Figures 6 and S8, the authors show the effects of Gyc76C knockdown in the female fat body on metabolism, feeding-associated behaviours and locomotor activity, which are interesting. Furthermore, the relevance of the phenotypes observed to potential in vivo actions of ITPa is explored in Figure 7. The authors conclude that "increased ITPa signaling results in phenotypes that largely mirror those seen following Gyc76C knockdown in the fat body, providing further support that ITPa mediates its effects via Gyc76C." Use of the term "largely mirror" seems inappropriate here because there are opposing effects- e.g. decreased starvation resistance in Figure 6A versus increased starvation resistance in Figure 7A. Furthermore, as discussed above, the results of these experiments do not prove that the effects of ITPa are mediated by Gyc76C because the effects reported here could be correlative, rather than causative. 

We thank this reviewer for an extremely thorough and fair assessment of our manuscript. 

We have now performed salt stress tolerance and chill coma recovery assays using flies over-expressing ITPa (new Figure 10 Supplement 1).

We agree that the use of the term “largely mirrors” to describe the effects of ITPa overexpression and Gyc76C knockdown is not appropriate and have changed this sentence. We also agree that the experiments did not provide direct evidence that the effects of ITPa are mediated by Gyc76C. To address this, we now provide evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Lastly, in Figures 8, S9, and S10 the authors analyse publicly available connectomic data and single-cell transcriptomic data to identify putative inputs and outputs of ITPa-expressing neurons. These data are a valuable addition to our knowledge ITPa expressing neurons; but they do not address the core hypothesis of this paper - namely that Gyc76C acts as an ITPa receptor.  

The goal of our study was to comprehensively characterize an anti-diuretic system in Drosophila. Hence, in addition to identifying the receptor via which ITPa exerts its effects, we also wanted to understand how ITPa-producing neurons are regulated. Connectomic and single-cell transcriptomic analyses are highly appropriate for this purpose. We have now updated the connectomic analyses using an improved connectome dataset that was released during the revision of this manuscript. Our new analysis shows that lNSC^ITP are connected to other endocrine cells that produce other homeostatic hormones (new Figure 13F). We also identify a pathway through which other ITP-producing neurons (LNd^ITP) receive hygrosensory inputs to regulate water seeking behavior (new Figure 13E). Moreover, we now include results which showcase that ITPa-producing neurons (l-NSC^ITP) are active (new Figure 8A and B) and release ITPa under desiccation. Together with other analyses, these data provide a comprehensive outlook on the when, what and how ITPa regulates systemic homeostasis.  

Strengths:  

(1) The main strengths of this paper are i) the detailed analysis of the expression and actions of ITP and the phenotypic consequences of overexpression of ITPa in Drosophila. ii). the detailed analysis of the expression of Gyc76C and the phenotypic consequences of knockdown of Gyc76C expression in Drosophila.  

(2) Furthermore, the paper is generally well-written and the figures are of good quality. 

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

Weaknesses:  

(1) The main weakness of this paper is that the data obtained do not prove that Gyc76C acts as a receptor for ITPa. Therefore, the following statement in the abstract is premature: "Using a phylogenetic-driven approach and the ex vivo secretion assay, we identified and functionally characterized Gyc76C, a membrane guanylate cyclase, as an elusive Drosophila ITPa receptor." Further experimental studies are needed to determine if Gyc76C acts as a receptor for ITPa. In the section of the paper headed "Limitations of the study", the authors recognise this weakness. They state "While our phylogenetic analysis, anatomical mapping, and ex vivo and in vivo functional studies all indicate that Gyc76C functions as an ITPa receptor in Drosophila, we were unable to verify that ITPa directly binds to Gyc76C. This was largely due to the lack of a robust and sensitive reporter system to monitor mGC activation." It is not clear what the authors mean by "the lack of a robust and sensitive reporter system to monitor mGC activation". The discovery of mGCs as receptors for ANP in mammals was dependent on the use of assays that measure GC activity in cells (e.g. by measuring cGMP levels in cells). Furthermore, more recently cGMP reporters have been developed. The use of such assays is needed here to investigate directly whether Gyc76C acts as a receptor for ITPa. In summary, insufficient evidence has been obtained to conclude that Gyc76C acts as a receptor for ITPa. Therefore, I think there are two ways forward, either:  

(a) The authors obtain additional biochemical evidence that ITPa is a ligand for Gyc76C.  

or  

(b) The authors substantially revise the conclusions of the paper (in the title, abstract, and throughout the paper) to state that Gyc76C MAY act as a receptor for ITPa, but that additional experiments are needed to prove this. 

We thank the reviewer for this comment and agree with the two options they propose. We had previously tried different a cGMP reporter (Promega GloSensor cGMP assay) to monitor activation of Gyc76C by ITPa in a heterologous system. Unfortunately, we were not successful in monitoring Gyc76C activation by ITPa. We now utilized another cGMP sensor, Green cGull, to show that ITPa can indeed activate Gyc76C heterologously expressed in HEK cells (new Figure 7 and Figure 7 Supplement 1). However, we still cannot rule out the possibility that ITPa can act on additional receptors in vivo. This is based on our ex vivo Malpighian tubule assays (new Figure 6E and F). ITPa inhibits DH31- and LK-stimulated secretion and we show that this effect is abolished in Gyc76C knockdown specifically in principal and stellate cells, respectively. Interestingly, application of ITPa alone can stimulate secretion when Gyc76C is knocked down in principal cells (new Figure 6E). This could be explained by: 1) presence of another receptor for ITPa which results in diuretic actions and/or 2) low Gyc76C signaling activity (RNAi based knockdown lowers signaling but does not abolish it completely) could alter other intracellular messenger pathways that promote secretion. We have added text to indicate the possibility of other ITPa receptors. Nonetheless, our conclusions are supported by the heterologous assay results which indicate that ITPa can activate Gyc76C. Therefore, we do not alter the title. 

(2) The authors state in the abstract that a phylogenetic-driven approach led to their identification of Gyc76C as a candidate receptor for ITPa. However, there are weaknesses in this claim. Firstly, because the hypothesis that Gyc76C may be involved in mediating effects of ITPa was first proposed ten years ago by Nagai et al. 2014, so this surely was the primary basis for investigating this protein. Nevertheless, investigating if there is correspondence in the phylogenetic distribution of ITP-type and Gyc76C-type genes/proteins is a valuable approach to addressing this issue. Unfortunately, the evidence presented is rather limited in scope. Essentially, the authors report that they only found ITP-type and Gyc76C-type genes/proteins in protostomes, but not in deuterostomes. What is needed is a more fine-grained analysis at the species level within the protostomes. Thus, are there protostome species in which both ITP-type and Gyc76C-type genes/proteins have been lost? Furthermore, are there any protostome species in which an ITP-type gene is present but an Gyc76C-type gene is absent, or vice versa? If there are protostome species in which an ITP-type gene is present but a Gyc76C-type gene is absent or vice versa, this would argue against Gyc76C being a receptor for ITPa. In this regard, it is noteworthy that in Figure 2A there are two ITP-type precursors in C. elegans, but there are no Gyc76Ctype proteins shown in the tree in Figure 2B. Thus, what is needed is a more detailed analysis of protostomes to investigate if there really is correspondence in the phylogenetic distribution of Gyc76C-type and ITP-type genes at the species level. 

We thank the reviewer for this comment. While the previous study by Nagai et al had implicated Gyc76C in the ITP signaling pathway, how they narrowed down Gyc76C as a candidate was not reported. Therefore, our unbiased phylogenetic approach was necessary to ensure that we identified all suitable candidate receptors. Indeed, our phylogenetic analysis also identified Gyc32E as another candidate ITP receptor. However, we did not pursue this receptor further as our expression data (new Figure 4 Supplement 2) indicated that Gyc32E is not expressed in osmoregulatory tissues and therefore likely does not mediate the osmotic effects of ITPa. 

We also appreciate the suggestion to perform a more detailed phylogenetic analysis for the peptide and receptor. We did not include C. elegans receptors in the phylogenetic analysis because they tend to be highly evolved and routinely cause long-branch attraction (see: Guerra and Zandawala 2024: https://doi.org/10.1093/gbe/evad108). We (specifically the senior author) have previously excluded C. elegans receptors in the phylogenetic analysis of GnRH and Corazonin receptors for similar reasons (see: Tian and Zandawala et al. 2016: 10.1038/srep28788). 

Unfortunately, absence of a gene in a genome is hard to prove especially when they are not as high-quality as the genomes of model systems (e.g. Drosophila and mice). Moreover, given the concern of this reviewer that our physiological and behavioral data on ITPa and Gyc76C only provide correlative evidence, we decided against performing additional phylogenetic analysis which also provides correlative evidence. Our only goal with this analysis was to identify a candidate ITPa receptor. Since we have now functionally characterized this receptor using a heterologous system, we feel that the current phylogenetic analysis was able to successfully serve its purpose.  

(3) The manuscript would benefit from a more comprehensive overview and discussion of published literature on Gyc76C in Drosophila, both as a basis for this study and for interpretation of the findings of this study.  

We thank the reviewer for this comment. We have now included a broader discussion of Gyc76C based on published literature.  

Reviewer #3 (Public Review):  

Summary:  

The goal of this paper is to characterize an anti-diuretic signaling system in insects using Drosophila melanogaster as a model. Specifically, the authors wished to characterize a role of ion transport peptide (ITP) and its isoforms in regulating diverse aspects of physiology and metabolism. The authors combined genetic and comparative genomic approaches with classical physiological techniques and biochemical assays to provide a comprehensive analysis of ITP and its role in regulating fluid balance and metabolic homeostasis in Drosophila. The authors further characterized a previously unrecognized role for Gyc76C as a receptor for ITPa, an amidated isoform of ITP, and in mediating the effects of ITPa on fluid balance and metabolism. The evidence presented in favor of this model is very strong as it combines multiple approaches and employs ideal controls. Taken together, these findings represent an important contribution to the field of insect neuropeptides and neurohormones and have strong relevance for other animals. 

We thank this reviewer for the positive and thorough assessment of our manuscript.

Strengths:  

Many approaches are used to support their model. Experiments were wellcontrolled, used appropriate statistical analyses, and were interpreted properly and without exaggeration.  

Weaknesses:  

No major weaknesses were identified by this reviewer. More evidence to support their model would be gained by using a loss-of-function approach with ITPa, and by providing more direct evidence that Gyc76C is the receptor that mediates the effects of ITPa on fat metabolism. However, these weaknesses do not detract from the overall quality of the evidence presented in this manuscript, which is very strong.  

We agree with this reviewer regarding the need to provide additional evidence using a loss-of-function approach with ITPa. We now characterize the phenotypes following knockdown of ITP in ITP-producing cells (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C. Unfortunately, we are not able to provide evidence that ITPa acts on Gyc76C in the fat body using the assay suggested by this reviewer (explained in detail below). Instead, we now provide direct evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Reviewer #1 (Recommendations For The Authors):  

Here, I have several extra concerns about the work as below:  

(1) The authors confirmed the function of ITPa in regulating both osmotic and metabolic homeostasis by specifically overexpressing ITPa driven by ITP-RCGal4 in adult flies (Figures. 5 and 7). Have authors ever tried to knock down ITP in ITP-RC-Gal4 neurons? What was the phenotype? Especially regarding the impact on metabolic homeostasis, does knocking down ITP in ITP neurons mimic the phenotypes of Gyc76C fat body knockdown flies? 

We thank the reviewer for this suggestion. We now characterize the phenotypes following knockdown of ITP using ITP-RC-Gal4 (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C.

The authors mentioned that the existing ITP RNAi lines target all three isoforms. It would be interesting if the authors could overexpress ITPa in ITPRC-Gal4>ITP-RNAi flies and confirm whether any phenotypes induced by ITP knockdown could be rescued. It will further confirm the role of ITPa in homeostasis regulation.  

We thank the reviewer for this suggestion. Unfortunately, this experiment is not straightforward because knockdown with ITP RNAi does not completely abolish ITP expression (see Figure 9A). Hence, the rescue experiment needs to be ideally performed in an ITP mutant background. However, ITP mutation leads to developmental lethality (unpublished observation) so we cannot generate all the flies necessary for this experiment. Therefore, we cannot perform the rescue experiments at this time. In future studies, we hope to perform knockdown of specific ITP isoforms using the transgenes generated here (Xu et al 2023: 10.1038/s41586-023-06833-8).   

(2) In Figures 5A and B, the authors nicely show the increased release of ITPa under desiccation by quantifying the ITPa immunolabelling intensity in different neuronal populations. It may be induced by the increased neuronal activity of ITPa neurons under the desiccated condition. Have the authors confirmed whether the activity of ITPa-expressing neurons is impacted by desiccation?  

The TRIC system may be able to detect the different activity of those neurons before and after desiccation. This may further explain the reduced ITPa peptide levels during desiccation.  

We thank the reviewer for this suggestion. We have now monitored the activity of ITPa-expressing neurons using the CaLexA system (Masuyama et al 2012: 10.3109/01677063.2011.642910). Our results indicate that ITPa neurons are indeed active under desiccation (new Figure 8A and B). These results are also in agreement with ITPa immunolabelling showing increased peptide release during desiccation (new Figure 8C and D). Together, these results show that ITPa neurons are activated and release ITPa under desiccation.  

(3) What about the intensity of ITPa immunolabelling in other ITPa-positive neurons (e.g., VNC) under desiccation? If there is no change in other ITPa neurons, it will be a good control. 

We thank the reviewer for this suggestion. Unfortunately, ITPa immunostaining in VNC neurons is extremely weak preventing accurate quantification of ITPa levels under different conditions. We did hypothesize that ITPa immunolabelling in clock neurons (5^th-LN_v and LN<Sub>d</sub>^ITP) would not change depending on the osmotic state of the animal. However, our results (Figure 8C and D) indicate that ITPa from these neurons is also released under desiccation. Interestingly, LNd^ITP, which also coexpress Neuropeptide F (NPF) have recently been implicated in water seeking during thirst (Ramirez et al, 2025: 10.1101/2025.07.03.662850). Our new connectomic-driven analysis shows that these neurons can receive thermo/hygrosensory inputs (new Figure 13E). Hence, it is conceivable that other ITPa-expressing neurons also release ITPa during thirst/desiccation.

(4) The adult stage, specifically overexpression of ITPa in ITP neurons, does show significant phenotypes compared to controls in both osmotic and metabolic homeostasis-related assays. It would be helpful if authors could show how much ITPa mRNA levels are increased in the fly heads with ITPa overexpression (under desiccation & starvation or not). 

We thank the reviewer for this suggestion. We have now included immunohistochemical evidence showing increase in ITPa peptide levels in flies with ITPa overexpression (new Figure 10A). We feel that this is a better indicator of ITPa signaling level instead of ITPa mRNA levels.   

(5) Another question concerns the bloated abdomens of ITPa-overexpressing flies. Are the bloated abdomens of ITPa OE female flies (Figure 5E) due to increased ovary size (Figure 7G)? Have the authors also detected similar bloated abdomens in male flies with ITPa overexpression? Since both male and female flies show more release of ITPa during the desiccation.  

We thank the reviewer for this comment. The bloated abdomen phenotype seen in females can be attributed to increased water content since we see a similar phenotype in males (see Author response image 1 below).

Author response image 1.

Reviewer #2 (Recommendations For The Authors):  

(1) Page 1 - change "Homeostasis is obtained by" to "Homeostasis is achieved by".  

Changed

(2) Page 1 - change "Physiological responses" to "Physiological processes". 

Changed

(3) Page 2 - Change "Recently, ITPL2 was also shown to mediate anti-diuretic effects via the tachykinin receptor" to "Recently, ITPL2 was also shown to exert anti-diuretic effects via the tachykinin receptor". 

Changed

(4) Page 9 - "(C) Adult-specific overexpression of ITPa using ITP- RC-GAL4TS (ITP-RC-T2A-GAL4 combined with temperature-sensitive tubulinGAL80) increases desiccation" Unless I am misunderstanding Fig 5C, I think what is shown is that overexpression of ITPa prolongs survival during a period of desiccation. I am not sure what the authors mean by "increases desiccation". In the text (page 9) the authors state "ITPa overexpression improves desiccation tolerance, which is a much clearer statement than what is in the figure legend. 

We thank the reviewer for identifying this oversight. We have now changed the caption to “increases desiccation tolerance”.  

(5) Page 11 - The authors conclude that "increased ITPa signaling results in phenotypes that largely mirror those seen following Gyc76C knockdown in the fat body, providing further support that ITPa mediates its effects via Gyc76C." Use of the term "largely mirror" seems inappropriate here because there are opposing effects- e.g. decreased starvation resistance in Figure 6A versus increased starvation resistance in Figure 7A.  

Perhaps there is a misunderstanding of what is meant by "mirroring" - it means the same, not the opposite. 

We thank the reviewer for this comment. We agree that the use of the term “largely mirrors” to describe the effects of ITPa overexpression and Gyc76C knockdown is not appropriate and have changed this sentence as follows: “Taken together, the phenotypes seen following Gyc76C knockdown in the fat body largely mirror those seen following ITP knockdown in ITP-RC neurons, providing further support that ITPa mediates its effects via Gyc76C.”

(6) Page 12 - There appear to be words missing between "neurons during desiccation, as well as their downstream" and "the recently completed FlyWire adult brain connectome" 

We thank the reviewer for highlighting this mistake. We have changed the sentence as following: “Having characterized the functions of ITP signaling to the renal tubules and the fat body, we wanted to identify the factors and mechanisms regulating the activity of ITP neurons during desiccation, as well as their downstream neuronal pathways. To address this, we took advantage of the recently completed FlyWire adult brain connectome (Dorkenwald et al., 2024, Schlegel et al., 2024) to identify pre- and post-synaptic partners of ITP neurons.”

(7) Page 15 - "can release up to a staggering 8 neuropeptides" - I suggest that the word "staggering" is removed. The notion that individual neurons release many neuropeptides is now widely recognised (both in vertebrates and invertebrates) based on analysis of single-cell transcriptomic data. 

Removed staggering.

(8) Page 16 - "(Farwa and Jean-Paul, 2024)" - this citation needs to be added to the reference list and I think it needs to be changed to "Sajadi and Paluzzi, 2024". 

We thank the reviewer for highlighting this oversight. The correct citation has now been added.

(9) It is noteworthy that, based on a PubMed search, there are at least thirteen published papers that report on Gyc76C in Drosophila (PMIDs: 34988396, 32063902, 27642749, 26440503, 24284209, 23862019, 23213443,  21893139, 21350862, 16341244, 15485853, 15282266, 7706258). However, none of these papers are discussed/cited by the authors. This is surprising because the authors' hypothesis that Gyc76C acts as a receptor for ITPa surely needs to be evaluated and discussed with reference to all the published insights into the developmental/physiological roles of this protein. 

We thank the reviewer for this comment. Some of the references mentioned above (21350862, 16341244, 15485853) mainly report on soluble guanylyl cyclases and not membrane guanylyl cyclase like Gyc76C. Based on other studies on Gyc76C and its role in immunity and development, we have now expanded the discussion on additional roles of ITPa.

Reviewer #3 (Recommendations For The Authors):  

I have only a few comments that will help the authors strengthen a couple of aspects of their model.  

(1) The case for Gyc76C as a receptor for ITPa in regulating fluid homeostasis is clear, given the experiments the authors carried out where they applied ITPa to tubules and showed that the effects of ITPa on tubule secretion were blocked if Gyc76C was absent in tubules. This approach, or something similar, should be used to provide conclusive proof that ITPa's metabolic effects on the fat body go through Gyc76C.  

At present (unless I missed it) the authors only show that gain of ITPa has the opposite phenotype to fat body-specific loss of Gyc76C. While this would be the expected result if ITPa/Gyc76C is a ligand-receptor pair, it is not quite sufficient to conclusively demonstrate that Gyc76C is definitely the fat body receptor. Ex vivo experiments such as soaking the adult fat body carcasses with and without Gyc76C in ITPa and monitoring fat content via Nile Red could be one way to address this lack of direct evidence. The authors could also make text changes to explicitly mention this lack of conclusive evidence and suggest it as a future direction.

We thank the reviewer for this comment. We have now conclusively demonstrated that Gyc76C is activated by ITPa in a heterologous assay (new Figure 7 and Figure 7 Supplement 1). With this evidence, we can confidently claim that ITPa can mediate its actions via Gyc76C in various tissues including the Malpighian tubules and fat body. Nonetheless, we liked the suggestion by this reviewer to perform the ex vivo assay and test the effect of ITPa on the fat body. Unfortunately, it is challenging to do this because increased ITPa signaling (chronically using ITPa overexpression) results in increased lipid accumulation in the fat body in vivo. Therefore, we would likely not see the effect of ITPa addition in an ex vivo fat body preparation since lipogenesis will not occur in the absence of glucose. However, ITPa could counteract the effects of other lipolytic factors such as adipokinetic hormone (AKH). To test this hypothesis, we monitored fat content in the fat body incubated with and without AKH (see Author response image 2 below showing representative images from this experiment). Since we did not observe any differences in fat levels between these two conditions, we were unable to test the effects of ITPa on AKH-activity using this assay.

Author response image 2.

(2) I did not see any loss of function data for ITPa - is this possible? If so this would strengthen the case for a 1:1 relationship between loss of ligand and loss of receptor. Alternatively, the authors could suggest this as an important future direction. 

We agree with this reviewer regarding the need to provide additional evidence using a loss-of-function approach with ITPa. We have now characterized the phenotypes following knockdown of ITP in ITP-producing cells (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C.

(3) For clarity, please include the sex of all animals in the figure legend. Even though the methods say 'females used unless otherwise indicated' it is still better for the reader to know within the figure legend what sex is displayed. 

We thank the reviewer for this suggestion and have now included sex of the animals in the figure legends.  

(4) Please state whether females are mated or not, as this is relevant for taste preferences and food intake. 

We apologize for this oversight. We used mated females for all experiments. This has now been included in the methods.  

(5) More discussion on the previous study on metabolic effects of ITP in this study compared with past studies would help readers appreciate any similarities and/or differences between this study and past work (Galikova 2018, 2022) 

We thank the reviewer for this suggestion. Unfortunately, it is difficult to directly compare our phenotypes with the metabolic effects of ITP reported in Galikova and Klepsatel 2022 because the previous study used a ubiquitous driver (Da-GAL4) to manipulate ITP levels. Ectopically overexpressing ITPa in non-ITP producing cells can result in non-physiological phenotypes. This is evident in their metabolic measurements where both global overexpression and knockdown of ITP results in reduced glycogen and fat levels, and starvation tolerance. Moreover, ITP-RC-GAL4 used in our study to overexpress and knockdown ITPa is more specific than the Da-GAL4 used previously. Da-GAL4 would include other ITP cells (e.g. ITP-RD producing cells). Since ITP is broadly expressed across the animal, it is difficult to parse out the phenotypes of ITPa and other isoforms using manipulations performed with Da-GAL4. We have mentioned this limitation in the results for ITP knockdown as follows: “A previous study employing ubiquitous ITP knockdown and overexpression suggests that Drosophila ITP also regulates feeding and metabolic homeostasis (Galikova and Klepsatel, 2022) in addition to osmotic homeostais (Galikova et al., 2018). However, given the nature of the genetic manipulations (ectopic ITPa overexpression and knockdown of ITP in all tissues) utilized in those studies, it is difficult to parse the effects of ITP signaling from ITPa-producing neurons.”

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

(1) Legionella effectors are often activated by binding to eukaryote-specific host factors, including actin. The authors should test the following: a) whether Lfat1 can fatty acylate small G-proteins in vitro; b) whether this activity is dependent on actin binding; and c) whether expression of the Y240A mutant in mammalian cells affects the fatty acylation of Rac3 (Figure 6B), or other small G-proteins.

We were not able to express and purify the full-length recombinant Lfat1 to perform fatty acylation of small GTPases in vitro. However, In cellulo overexpression of the Y240A mutant still retained ability to fatty acylate Rac3 and another small GTPase RheB (see Figure 6-figure supplement 2). We postulate that under infection conditions, actin-binding might be required to fatty acylate certain GTPases due to the small amount of effector proteins that secreted into the host cell.

(2) It should be demonstrated that lysine residues on small G-proteins are indeed targeted by Lfat1. Ideally, the functional consequences of these modifications should also be investigated. For example, does fatty acylation of G-proteins affect GTPase activity or binding to downstream effectors?

We have mutated K178 on RheB and showed that this mutation abolished its fatty acylation by Lfat1 (see Author response image 1 below). We were not able to test if fatty acylation by Lfat1 affect downstream effector binding.

Author response image 1.

(3) Line 138: Can the authors clarify whether the Lfat1 ABD induces bundling of F-actin filaments or promotes actin oligomerization? Does the Lfat1 ABD form multimers that bring multiple filaments together? If Lfat1 induces actin oligomerization, this effect should be experimentally tested and reported. Additionally, the impact of Lfat1 binding on actin filament stability should be assessed. This is particularly important given the proposed use of the ABD as an actin probe.

The ABD domain does not form oligomer as evidenced by gel filtration profile of the ABD domain. However, we do see F-actin bundling in our in vitro -F-actin polymerization experiment when both actin and ABD are in high concentration (data not shown). Under low concentration of ABD, there is not aggregation/bundling effect of F-actin.

(4) Line 180: I think it's too premature to refer to the interaction as having "high specificity and affinity." We really don't know what else it's binding to.

We have revised the text and reworded the sentence by removing "high specificity and affinity."

(5) The authors should reconsider the color scheme used in the structural figures, particularly in Figures 2D and S4.

Not sure the comments on the color scheme of the structure figures.

(6) In Figure 3E, the WT curve fits the data poorly, possibly because the actin concentration exceeds the Kd of the interaction. It might fit better to a quadratic.

We have performed quadratic fitting and replaced Figure 3E.

(7) The authors propose that the individual helices of the Lfat1 ABD could be expressed on separate proteins and used to target multi-component biological complexes to F-actin by genetically fusing each component to a split alpha-helix. This is an intriguing idea, but it should be tested as a proof of concept to support its feasibility and potential utility.

It is a good suggestion. We plan to thoroughly test the feasibility of this idea as one of our future directions.

(8) The plot in Figure S2D appears cropped on the X-axis or was generated from a ~2× binned map rather than the deposited one (pixel size ~0.83 Å, plot suggests ~1.6 Å). The reported pixel size is inconsistent between the Methods and Table 1-please clarify whether 0.83 Å refers to super-resolution.

Yes, 0.83 Å is super-resolution.  We have updated in the cryoEM table

Reviewer #2:

Weaknesses:

(1) The authors should use biochemical reactions to analyze the KFAT of Llfat1 on one or two small GTPases shown to be modified by this effector in cellulo. Such reactions may allow them to determine the role of actin binding in its biochemical activity. This notion is particularly relevant in light of recent studies that actin is a co-factor for the activity of LnaB and Ceg14 (PMID: 39009586; PMID: 38776962; PMID: 40394005). In addition, the study should be discussed in the context of these recent findings on the role of actin in the activity of L. pneumophila effectors.

We have new data showed that Actin binding does not affect Lfat1 enzymatic activity. (see response to Reviewer #1). We have added this new data as Figure S7 to the paper. Accordingly, we also revised the discussion by adding the following paragraph.

“The discovery of Lfat1 as an F-actin–binding lysine fatty acyl transferase raised the intriguing question of whether its enzymatic activity depends on F-actin binding. Recent studies have shown that other Legionella effectors, such as LnaB and Ceg14, use actin as a co-factor to regulate their activities. For instance, LnaB binds monomeric G-actin to enhance its phosphoryl-AMPylase activity toward phosphorylated residues, resulting in unique ADPylation modifications in host proteins  (Fu et al, 2024; Wang et al, 2024). Similarly, Ceg14 is activated by host actin to convert ATP and dATP into adenosine and deoxyadenosine monophosphate, thereby modulating ATP levels in L. pneumophila–infected cells (He et al, 2025). However, this does not appear to be the case for Lfat1. We found that Lfat1 mutants defective in F-actin binding retained the ability to modify host small GTPases when expressed in cells (Figure S7). These findings suggest that, rather than serving as a co-factor, F-actin may serve to localize Lfat1 via its actin-binding domain (ABD), thereby confining its activity to regions enriched in F-actin and enabling spatial specificity in the modification of host targets.”

(2) The development of the ABD domain of Llfat1 as an F-actin domain is a nice extension of the biochemical and structural experiments. The authors need to compare the new probe to those currently commonly used ones, such as Lifeact, in labeling of the actin cytoskeleton structure.

We fully agree with the reviewer’s insightful suggestion. However, a direct comparison of the Lfat1 ABD domain with commonly used actin probes such as Lifeact, as well as evaluation of the split α-helix probe (as suggested by Reviewer #1), would require extensive and technically demanding experiments. These are important directions that we plan to pursue in future studies.

For all other minors, we have made corrections/changes in our revised text and figures.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

What are the overarching principles by which prokaryotic genomes evolve? This fundamental question motivates the investigations in this excellent piece of work. While it is still very common in this field to simply assume that prokaryotic genome evolution can be described by a standard model from mathematical population genetics, and fit the genomic data to such a model, a smaller group of researchers rightly insists that we should not have such preconceived ideas and instead try to carefully look at what the genomic data tell us about how prokaryotic genomes evolve. This is the approach taken by the authors of this work. Lacking a tight theoretical framework, the challenge of such approaches is to devise analysis methods that are robust to all our uncertainties about what the underlying evolutionary dynamics might be.

The authors here focus on a collection of ~300 single-cell genomes from a relatively well-isolated habitat with relatively simple species composition, i.e. cyanobacteria living in hotsprings in Yellowstone National Park, and convincingly demonstrate that the relative simplicity of this habitat increases our ability to interpret what the genomic data tells us about the evolutionary dynamics.

Using a very thorough and multi-faceted analysis of these data, the authors convincingly show that there are three main species of Synechococcus cyanobacteria living in this habitat, and that apart from very frequent recombination within each species (which is in line with insights from other recent studies) there is also a remarkably frequent occurrence of hybridization events between the different species, and with as of yet unidentified other genomes. Moreover, these hybridization events drive much of the diversity within each species. The authors also show convincing evidence that these hybridization events are not neutral but are driven by selected by natural selection.

Strengths:

The great strength of this paper is that, by not making any preconceived assumptions about what the evolutionary dynamics is expected to look like, but instead devising careful analysis methods to tease apart what the data tells us about what has happened in the evolution in these genomes, highly novel and unexpected results are obtained, i.e. the major role of hybridization across the 3 main species living in this habitat.

The analysis is very thorough and reading the detailed supplementary material it is clear that these authors took a lot of care in devising these methods and avoiding the pitfalls that unfortunately affect many other studies in this research area.

The picture of the evolutionary dynamics of these three Synechococcus species that emerge from this analysis is highly novel and surprising. I think this study is a major stepping stone toward the development of more realistic quantitative theories of genome evolution in prokaryotes.

The analysis methods that the authors employ are also partially novel and will no doubt be very valuable for analysis of many other datasets.

We thank the reviewer for their appreciation of our work.

Weaknesses:

I feel the main weakness of this paper is that the presentation is structured such that it is extremely difficult to read. I feel readers have essentially no chance to understand the main text without first fully reading the 50-page supplement with methods and 31 supplementary materials. I think this will unfortunately strongly narrow the audience for this paper and below in the recommendations for the authors I make some suggestions as to how this might be improved.<br /> A very interesting observation is that a lot of hybridization events (i.e. about half) originate from species other than the alpha, beta, and gamma Synechococcus species from which the genomes that are analyzed here derive. For this to occur, these other species must presumably also be living in the same habitat and must be relatively abundant. But if they are, why are they not being captured by the sampling? I did not see a clear explanation for this very common occurrence of hybridization events from outside of these Synechococcus species. The authors raise the possibility that these other species used to live in these hot springs but are now extinct. I'm not sure how plausible this is and wonder if there would be some way to find support for this in the data (e.g that one does not observe recent events of import from one of these unknown other species). This was one major finding that I believe went without a clear interpretation.

We agree with the reviewer that the extent of hybridization with other species is surprising. While we do feel that our metagenome data provide convincing evidence that “X” species are not present in MS or OS, we cannot currently rule out the presence of X in other springs. In the revision we explicitly mention the alternative hypothesis (Lines 239-242).

The core entities in the paper are groups of orthologous genes that show clear evidence of hybridization. It is thus very frustating that exactly the methods for identifying and classifying these hybridization events were really difficult to understand (sections I and V of the supplement). Even after several readings, I was unsure of exactly how orthogroups were classified, i.e. what the difference between M and X clusters is, what a `simple hybrid' corresponds to (as opposed to complex hybrids?), what precisely the definitions of singlet and non-singlet hybrids are, etcetera. It also seems that some numbers reported in the main text do not match what is shown in the supplement. For example, the main text talks about "around 80 genes with more than three clusters (SM, Sec. V; fig. S17).", but there is no group with around 80 genes shown in Fig S17! And similarly, it says "We found several dozen (100 in α and 84 in β) simple hybrid loci" and I also cannot match those numbers to what is shown in the supplement. I am convinced that what the authors did probably made sense. But as a reader, it is frustrating that when one tries to understand the results in detail, it is very difficult to understand what exactly is going on. I mention this example in detail because the hybrid classification is the core of this paper, but I had similar problems in other sections.

We thank the reviewer for pointing out these issues with our original presentation. In the revision, we have redone most of the analysis to simplify the methods and check the consistency of the results. We did not find any qualitative differences in our results after reanalysis, but some of the numbers for different hybridization patterns have changed. The most notable difference is an increase in the number of alpha-gamma simple hybrids and a corresponding decrease in mixed-species clusters (now labeled mosaic hybrids). These transfers are difficult to assign because we only have access to a single gamma genome. We have added a short explanation of this point in Lines 219-222.

To improve the presentation, we significantly expanded the “Results” section to better explain our analysis and the different steps we take. We included two additional figures (Figs. 3 and 4) that illustrate the different types of hybrids and the heterogeneity in the diversity of alpha which is discussed in the main text and is important for interpreting our results. We also included two additional figures (Figs. 2 and 6) that were previously in the Appendix but were mentioned in the main text. We believe these changes should address most of the issues raised by the reviewer and hopefully make the manuscript easier to read.

Although I generally was quite convinced by the methods and it was clear that the authors were doing a very thorough job, there were some instances where I did not understand the analysis. For example, the way orthogroups were built is very much along the lines used by many in the field (i.e. orthoMCL on the graph of pairwise matchings, building phylogenies of connected components of the graph, splitting the phylogenies along long branches). But then to subdivide orthogroups into clusters of different species, the authors did not use the phylogenetic tree already built but instead used an ad hoc pairwise hierarchical average linkage clustering algorithm.

The reviewer is correct that there is an unexplained discrepancy between the clustering methods we used at different steps in our pipeline. We followed previous work by using phylogenetic distances for the initial clustering of orthogroups. On these scales we expect hybridization to play a minor role and phylogenetic distances to correlate reasonably well with evolutionary divergence. However, because of the extensive hybridization we observed, the use of phylogenetic models for species clustering is more difficult to justify. We therefore chose to simply use pairwise nucleotide distances, which make fewer assumptions about the underlying evolutionary processes and should be more robust. We have briefly explained our reasoning and the details of our clustering method in the revision (Lines 182-190).

Reviewer #2 (Public Review):

Summary:

Birzu et al. describe two sympatric hotspring cyanobacterial species ("alpha" and "beta") and infer recombination across the genome, including inter-species recombination events (hybridization) based on single-cell genome sequencing. The evidence for hybridization is strong and the authors took care to control for artefacts such as contamination during sequencing library preparation. Despite hybridization, the species remain genetically distinct from each other. The authors also present evidence for selective sweeps of genes across both species - a phenomenon which is widely observed for antibiotic resistance genes in pathogens, but rarely documented in environmental bacteria.

Strengths:

This manuscript describes some of the most thorough and convincing evidence to date of recombination happening within and between cohabitating bacteria in nature. Their single-cell sequencing approach allows them to sample the genetic diversity from two dominant species. Although single-cell genome sequences are incomplete, they contain much more information about genetic linkage than typical short-read shotgun metagenomes, enabling a reliable analysis of recombination. The authors also go to great lengths to quality-filter the single-cell sequencing data and to exclude contamination and read mismapping as major drivers of the signal of recombination.

We thank the reviewer for their appreciation of our work.

Weaknesses:

Despite the very thorough and extensive analyses, many of the methods are bespoke and rely on reasonable but often arbitrary cutoffs (e.g. for defining gene sequence clusters etc.). Much of this is warranted, given the unique challenges of working with single-cell genome sequences, which are often quite fragmented and incomplete (30-70% of the genome covered). I think the challenges of working with this single-cell data should be addressed up-front in the main text, which would help justify the choices made for the analysis.

We have significantly expanded the “Results” section to better justify and explain the choices we made during our analysis. We hope these changes address the reviewer’s concerns and make the manuscript more accessible to readers.

The conclusions could also be strengthened by an analysis restricted to only a subset of the highest quality (>70% complete) genomes. Even if this results in a much smaller sample size, it could enable more standard phylogenetic methods to be applied, which could give meaningful support to the conclusions even if applied to just ~10 genomes or so from each species. By building phylogenetic trees, recombination events could be supported using bootstraps, which would add confidence to the gene sequence clustering-based analyses which rely on arbitrary cutoffs without explicit measures of support.

It seems to us that the reviewer’s suggestion presupposes that the recombination events we find can be described as discrete events on an asexual phylogeny, similar to how rare mutations are treated in standard phylogenetic inference. Popular tools, such as ClonalFrame and its offshoots, have attempted to identify individual recombination events starting from these assumptions. But the main conclusion of both our linkage and SNP block analysis is that the ClonalFrame assumptions do not hold for our data. Under a clonal frame, the SNP blocks we observe should be perfectly linked, similar to mutations on an asexual tree. But our results in Fig. 7D show the opposite. Part of the issue may have been that in our original presentation, we only briefly discuss the results of our linkage analysis and refer readers to the Appendix for more details. To fix this issue we have added an extra figure (Fig. 2), showing rapid linkage decrease in both species and that at long distances the linkage values are essentially identical to the unlinked case, similar to sexual populations. We hope that this change will help clarify this point.

The manuscript closes without a cartoon (Figure 4) which outlines the broad evolutionary scenario supported by the data and analysis. I agree with the overall picture, but I do think that some of the temporal ordering of events, especially the timing of recombination events could be better supported by data. In particular, is there evidence that inter-species recombination events are increasing or decreasing over time? Are they currently at steady-state? This would help clarify whether a newly arrived species into the caldera experiences an initial burst of accepting DNA from already-present species (perhaps involving locally adaptive alleles), or whether recombination events are relatively constant over time.

The reviewer raises some very interesting questions about the dynamics of recombination in the population, which we hope to pursue in future work. We have added this as an open question in the Discussion (Lines 365-382).

These questions could be answered by counting recombination events that occur deeper or more recently in a phylogenetic tree.

The reviewer here seems to presuppose that recombination is rare enough that a phylogenetic tree can reliably be inferred, which is contrary to our linkage analysis (see the response to an earlier comment). Perhaps the reviewer missed this point in our original manuscript since it was discussed primarily in the Appendix. See also our response to a previous comment by the reviewer.

The cartoon also shows a 'purple' species that is initially present, then donates some DNA to the 'blue' species before going extinct. In this model, 'purple' DNA should also be donated to the more recently arrived 'orange' species, in proportion to its frequency in the 'blue' genome. This is a relatively subtle detail, but it could be tested in the real data, and this may actually help discern the order of the inferred recombination events.

We have included an extra figure in the main text (Fig. 6) that addresses the question of timing of events. A quantitative test of our cartoon model along the lines the reviewer suggested would certainly be worthwhile and we hope to do that in future work.  

The abstract also makes a bold claim that is not well-supported by the data: "This widespread mixing is contrary to the prevailing view that ecological barriers can maintain cohesive bacterial species..." In fact, the two species are cohesive in the sense that they are identifiable based on clustering of genome-wide genetic diversity (as shown in Fig 1A). I agree that the mixing is 'widespread' in the sense that it occurs across the genome (as shown in Figure 2A) but it is clearly not sufficient to erode species boundaries. So I believe the data is consistent with a Biological Species Concept (sensu Bobay & Ochman, Genome Biology & Evolution 2017) that remains 'fuzzy' - such that there are still inter-species recombination events, just not sufficient to erode the cohesion of genomic clusters. Therefore, I think the data supports the emerging picture of most bacteria abiding by some version of a BSC, and is not particularly 'contrary' to the prevailing view.

We have revised the phrase mentioned by the reviewer to “prevent genetic mixture between bacterial species,” which more accurately represents our conclusions. 

The final Results paragraph begins by posing a question about epistatic interactions, but fails to provide a definitive answer to the extent of epistasis in these genomes. Quantifying epistatic effects in bacterial genomes is certainly of interest, but might be beyond the scope of this paper. This could be a Discussion point rather than an underdeveloped section of the Results.

We agree with the reviewer that an exhaustive analysis of epistasis in the population is beyond the scope of the manuscript. Our original intention was to answer whether SNP blocks we discovered showed evidence of strong linkage, as might be expected if only a small number of strains are present in the population. In light of the previous comments by the reviewer regarding the consistency with the clonal frame hypothesis, we believe this is especially relevant for our results. Moreover, the results we found‑especially for the beta population‑were quite conclusive: SNP block linkages in beta are indistinguishable from an unlinked model. To avoid misdirecting the reader about the significance of our results, we have revised the relevant paragraph (Lines 316-319).

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

Although I am entirely convinced of the validity of the results, methodology, and interpretations presented in this work, I must say I found the paper very hard to read. And I think I am really quite familiar with these kinds of approaches. I fear that for people other than experts on these kinds of comparative genomic analyses, this paper will be almost impossible to read. With the aim of expanding the audience for this compelling work, I think the authors might want to consider ways to improve the presentation.

At the end of a long project, the obtained results typically form a web of mutual interconnections and dependencies and one of the key challenges in presenting the results in a paper is having to untangle this web of connected results and analysis into a linear ordered narrative so that, at any point in the narrative, understanding the next point only depends on previous points in the narrative. I frankly feel that this paper fails at this.

The paper reads to me as if one author put together the supplement by essentially writing a report of all the analyses that were done together with supplementary figures summarizing all those analyses, and that another author then wrote the main text by using the materials in the supplement almost in the way a cook uses ingredients for a dish. Almost every other sentence in the main text refers to results in the (31!) supplementary figures and can only be understood by reading the appropriate corresponding sections in the supplementary materials. I found it essentially impossible to read the main text without having first read the entire 50-page supplement.

I think the paper could be hugely improved by trying to restructure the presentation so as to make it more linear. The main text can be expanded to include a summary of the crucial methods and analysis results from the supplement needed to understand the narrative in the main text. For example, as it currently stands it is really challenging to understand what is shown in figures 2 and 3 of the main text without having to first read a very substantial part of the supplement. Figure 3, even after having read the relevant sections in the supplement, took me quite a while to understand and almost felt like a puzzle to decypher. Rethinking which parts of the supplement are really necessary would also help. Finally, it would also help if the terminology was kept as simple, transparent, and consistent as possible.

I understand that my suggestion to thoroughly reorganize the presentation may feel like a big hassle, but I am afraid that in its current form, these important results are essentially rendered inaccessible to all but a small group of experts in this area. This paper deserves a wider readership.

We thank the reviewer for these valuable suggestions. In the revision, we have significantly expanded and restructured the “Results” section to make the presentation more linear, as the reviewer suggested (see our reply to the public comment by the reviewer for details). We hope these changes will make the manuscript easier to read.

Reviewer #2 (Recommendations For The Authors):

I found this paper challenging to follow since the main text was so condensed and the supplementary material so extensive. Given that eLife does not impose strong limits on the length of the main text, I suggest moving some key sections from the supplement into the main text to make it easier for the reader to follow rather than flipping back and forth. Adding to the confusion, supplementary figures were referenced out of order in the main text (e.g. S23 is referenced before S1). Please check the numbering and ensure figures are mentioned in the main text in the correct order.

We thank the reviewer for their feedback on the presentation of the results. In response to similar comments from Reviewer #1, we have significantly expanded and restructured the “Results” section to make it easier to read (see also our responses to Reviewer #1).

Page 2: The term 'coevolution' is typically reserved for two species that mutually impose selective pressures on one another (e.g. predator-prey interactions; see Janzen, Evolution 1980). In the context of these two cyanobacterial species, it's not clear that this is the case so I would simply refer to them 'cohabitating' or being sympatric in the same environment.

It is true that the term "coevolution” has become associated with predator-prey interactions, as the reviewer said. However, we feel that in our case “coevolution” fairly accurately describes the continual hybridization over long time scales we observe. We have therefore chosen to keep the term.

Page 3: The authors mention that the gamma SAG is ~70% complete, which turns out to be quite high. It would be useful to mention early in the Results the mean/median completeness across SAGs, and how this leads to some challenges in analysing the data. Some of the material from the Supplement could be moved into the Results here.

We have added a short note on the completeness in the Results (Lines 153-154). We have also added an extra figure in Appendix 1 with the completeness of all the SAGs for interested readers.

I was left puzzled by the sentence: "Alternatively, high rates of recombination could generate different genotypes within each genome cluster that are adapted to different temperatures, with the relative frequencies of each cluster being only a correlated and not a causal driver of temperature adaptation." This is suggesting that individual genes or alleles, rather than entire genomes, could be adapted to temperature. But figure 1B seems to imply that the entire genome is adapted to different temperatures. Anyway, this does not seem to be a key point and could probably be removed (or clarified if the authors deem this an important point, which I failed to understand).

We have revised this section to clarify the alternative hypothesis mentioned by the reviewer (Lines 100-103).

Page 4. 'Several dozen' hybrid genes were found, but please also specify how many genes were tested. In general, it would be good to briefly outline the sample size (SAGs or genes) considered for each analysis.

We have added the total numbers of genes we analyzed at each step of our analysis.

'Mosaic hybrid loci' are mentioned alongside the issue of poor alignment. Presumably, the mosaic hybrid loci are first filtered to remove the poor alignments? This should be specified, and please mention how many loci are retained before/after this filter.

We thank the reviewer for highlighting this important point. In the revision, we have implemented a more aggressive filtering of genes with poor alignments. We have added an extra paragraph to Appendix 1 (step 5 in the pipeline analysis) briefly explaining the issue.

Page 5. "By contrast, the diversity of mosaic loci was typical of other loci within beta, suggesting most of the beta genome has undergone hybridization." Please point to the data (figure) to support this statement.

We have restructured our discussion of the different hybrid loci so this comment is no longer relevant. In case the reviewer is interested, the synonymous diversity within beta was 0.047, while in mosaic hybrids it was 0.064.

Page 6. "The largest diversity trough contained 28 genes." Since this trough is discussed in detail and seems to be of interest, it would be nice to illustrate it, perhaps as an inset in Figure 2 or as a separate figure. If I understood correctly, this trough includes genes (in a nitrogen-fixation pathway) that are present in all genomes, but are exchanged by homologous recombination. So I don't think it's correct to say that the "ancestors acquired the ability to fix nitrogen." Rather, the different alleles of these same genes were present in the ancestor. So perhaps there was a selective sweep involving alleles in this region that provided adaptation to local nitrogen sources or concentrations, but not a gain of new genes. Perhaps I misunderstood, in which case clarification would be appreciated.

The reviewer raises an interesting possibility. We agree that it is in principle possible that the ancestor contained the nitrogen fixation genes and the selective sweep simply replaced the ancestral alleles. In this particular case, there is additional evidence that the entire pathway was acquired around roughly the same time from gene order. The gene order between alpha and beta is almost entirely different, with only a few segments containing more than 2-3 genes in the same order, as shown by Bhaya et al. 2007 and confirmed by additional unpublished analysis of the SAGs. One of the few exceptions is the nitrogen fixation pathway, which has essentially the same gene order over more than 20 kbp. Thus, if the ancestor of both alpha and beta contained the nitrogen-fixation pathway, we would expect these genes to be scatter across the genome. We have revised the sentences in question to clarify this point (Lines 260-271).

Page 6. Last paragraph on epistasis references Fig 3C, but I believe it should be Fig 3D.

Fixed.

Page 7. Figure 3 legend. "Note that alpha-2 is identical to gamma here." I believe it should be beta, not gamma.

The reviewer is correct. We have fixed this error.

Page 8. What is the evidence for "at least six independent colonizers"? I could not find the data supporting this claim.

The statement mentioned by the reviewer was based on the maximum number of species clusters we identified in different core genes. However, during the revision, we found that only a handful of genes contained five or more clusters. We did find several tens of genes with four clusters. In addition, Rosen et al. (2018) also found additional 16S clusters at low frequency in the same springs. Based on these results we conservatively estimate that at least four independent strains colonized the caldera, but the number could be much greater. We have revised the text in question accordingly (Lines 336-339) and added Fig. 2 in Appendix 1 to support the conclusion.

Page 9. Line 200: "acting to homogenize the population." It should be specified that the population is only homogenized at these introgressed loci, not genome-wide. Otherwise, the genome-wide species clusters seen in Fig 1 would not be maintained.

It is true that the selective sweeps that lead to diversity throughs only homogenize the introgressed loci. But other hybrid segments could also rise to high frequency in the population during the sweep through hitchhiking. The fact that we observe SNP blocks generated through secondary recombination events of introgressed segments throughout the genome supports this view. While we do not fully understand the dynamics of this process currently, we do feel that the current evidence supports the statement that mixing is occurring throughout the genome and not just at a few loci so we have kept the original statement.

The final sentence (lines 221-222) is vague and uninformative. On the one hand, "investigating whether hybridization plays a major role" is what the current manuscript has already done - depending on what is meant by 'major' (how much of the genome? Or whether there are ecological implications?). It is also not clear what is meant by a predictive theory and 'possible evolutionary scenarios. This should be elaborated upon, otherwise, it is not clear what the authors mean. Otherwise, this sentence could be cut.

We thank the reviewer for their feedback. One possible source of confusion could be that in this sentence we were referring to detecting hybridization in other communities. We have changed “these communities” to “other communities” to make this clearer.

Supplement.

Broadly speaking, I appreciate the thorough and careful analysis of the single cell data. On the other hand, it is hard to evaluate whether these custom analyses are doing what is intended in many cases. Would it be possible to consider an analysis using more established methods, e.g. taking a subset of genomes with 'good' completeness and using Panaroo to find the core and accessory genome, then ClonalFrameML or Gubbins to infer a phylogeny and recombination events? Such analyses could probably be applied to a subset of the sample with relatively complete genomes. I don't want to suggest an overly time-consuming analysis, but the authors could consider what would be feasible.

We have added a comparison between our analysis and that from two other methods, including ClonalFrameML mentioned by the author. One important point that we feel might have been lost in the first version is that our linkage results imply that recombination is not rare such that it can be mapped onto an asexual tree as assumed by ClonalFrameML. Note that this is not simply due to technical limitations due to incomplete coverage and is instead a consequence of the evolutionary dynamics of the population. Consistent with this, we found several inconsistencies in how recombination events were assigned by ClonalFrameML. We have summarized these conclusions in Appendix 7 of the revised manuscript.

Page 8. Line 190. What is meant by 'minimal compositional bias'?

We mean that the sample is not biased towards strains that grow in the lab. We have revised the sentence to clarify.

Page 25. Figure S14 is not referenced in the text.

We have added part of this figure to the main text since it illustrates one of our main results, namely that sites at long genomic distances are essentially unlinked.

Page 26. The 'unlinked controls' (line 530) are very useful, but it would be even more informative to see if these controls also show the same decline in linkage with distance in the genome as observed in the real data. In particular, it would be good to know if the observed rapid decline in linkage with distance in the low-diversity regions is also observed in controls. Currently, it is unclear if this observation might be due to higher uncertainty in inferring linkage in low-diversity regions, which by definition have less polymorphism to include in the linkage calculation.

We thank the reviewer for the suggestion. After further consideration, we have decided to remove the subsection on linkage decrease in the low-diversity regions. We feel such detailed quantitative analysis would be better suited for a more technical paper, which we hope to do at a later time.

Page 26. There are some sections with missing identifiers (Sec ??).

Fixed.

Page 27. The information about the typical breadth of SAG coverage (~30%) would be better to include earlier in the Supplement, and also mentioned in the main text so the reader can more easily understand the nature of the dataset.

We have added an extra figure with the SAG coverages to Appendix 1.

Page 29. Any sensitivity analysis around the S = 0.9 value? Even if arbitrary, could the authors provide justification why they think this value is reasonable?

We have significantly revised this section in response to earlier comments by one of the reviewers. We hope that this would clarify the details of our methods to interested readers. To answer the reviewer’s specific question, we chose this heuristic after examining the fraction of cells of each species in different species clusters. For the clusters assigned to alpha and beta, we found a sharp peak near one and that a cutoff of 0.9 captured most clusters while still being high enough to inconsistent with a mixed cluster.

Page 30. I could not see where Fig. S17 was mentioned in the text. Also, how are 'simple hybrid genes' defined?

We have removed this figure in the revision. The definition of the different types of hybrid genes have been added to the main text in response to a comment from the other reviewer.

Page 36. It is hard to see that divergence is 'high' relative to what reference. Would it be possible to include the expected value (from ref. 12) in the plot, or at least explicitly mentioned in the text?

We have added the mean synonymous and non-synonymous divergences between alpha and beta to the figures for reference.

Page 38. Line 770 "would be comparable to that of beta." This is not necessarily the case since beta could have a different time to its most recent common ancestor. It could have a different time to the last bottleneck or selective sweep, etc.

We thank the reviewer for pointing out this misleading statement. Our point here was that in the first scenario the TMRCA of alpha and beta would be similar since the diversity in the high-diversity alpha genes is similar to beta. We have clarified this statement in the revision.

Page 39. Line 793. The use of the term 'genomic backbone' implies the presence of a clonal frame, which is not what the data seems to support. Perhaps another term such as 'genetic diversity' would more appropriately capture the intended meaning here.

We agree with the reviewer that the low-diversity regions may not be asexual. We used “genomic backbone” to distinguish from the “clonal frame,” which is usually used to mean that the backbone is asexual. We have added a note in the revision to clarify this point.

Page 39. Lines 802-805. I found this explanation hard to follow. Could the logic be clarified?

We simply meant that although the beta distribution is unimodal, it is not consistent with a simple Poisson distribution, unlike in alpha. We have added an extra sentence to clarify this.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

In this valuable manuscript, Lin et al attempt to examine the role of long non coding RNAs (lncRNAs) in human evolution, through a set of population genetics and functional genomics analyses that leverage existing datasets and tools. Although the methods are incomplete and at times inadequate, the results nonetheless point towards a possible contribution of long non coding RNAs to shaping humans, and suggest clear directions for future, more rigorous study.

Comments on revisions:

I thank the authors for their revision and changes in response to previous rounds of comments. As it had been nearly two years since I last saw the manuscript, I reread the full text to familiarise myself again with the findings presented. While I appreciate the changes made and think they have strengthened the manuscript, I still find parts of it a bit too speculative or hyperbolic. In particular, I think claims of evolutionary acceleration and adaptation require more careful integration with existing human/chimpanzee genetics and functional genomics literature.

We thank the reviewer heartfully for the great patience and valuable comments, which have helped us further improve the manuscript. Before responding to comments point by point, we provide a summary here.

(1) On parameters and cutoffs.

Parameters and cutoffs influence data analysis. The large number of Supplementary Notes, Supplementary Figures, and Supplementary Tables indicates that we paid great attention to the influence of parameters and robustness of analyses. Specifically, here we explain the DBS sequence distance cutoff of 0.034, which determines the top 20% genes that most differentiate humans from chimpanzees and influences the gene set enrichment analysis (Figure 2). As described in the revised manuscript, we estimated this cutoff based on Song et al., verified its rationality based on Prufer et al. (Song et al. 2021; Prufer et al. 2017), and measured its influence by examining slightly different cutoff values (e.g., 0.035).

(2) Analyses of HS TFs and HS TF DBSs.

It is desirable to compare the contribution of HS lncRNAs and HS TFs to human evolution. Identifying HS TFs faces the challenges that different institutions (e.g., NCBI and Ensembl) annotate orthologous genes using different criteria, and that multiple human TF lists have been published by different research groups. Recently, Kirilenko et al. identified orthologous genes in hundreds of placental mammals and birds and organized different types of genes into datasets of parewise comparison (e.g., hg38-panTro6) using humans and mice as references (Kirilenko et al. Integrating gene annotation with orthology inference at scale. Science 2023). Based on (a) the many2zero and one2zero gene lists in the “hg38-panTro6” dataset, (b) three human TF lists reported by two studies (Bahram et al. 2015; Lambert et al. 2018) and used in the SCENIC package, we identified HS TFs. The number of HS TFs and HS lncRNAs (5 vs 66) alone lends strong evidence suggesting that HS lncRNAs have contributed more significantly to human evolution than HS TFs (note that 5 is the union of three intersections between <many2zero + one2zero> and the three <human TF list>).

TF DBS (i.e., TFBS) prediction has also been challenging because they are very short (mostly about 10 bp) and TF-DNA binding involves many cofactors (Bianchi et al. Zincore, an atypical coregulator, binds zinc finger transcription factors to control gene expression. Science 2025). We used two TF DBS prediction programs to predict HS TF DBSs, including the well-established FIMO program (whose results have been incorporated into the JASPAR database) (Rauluseviciute et al. JASPAR 2024: 20th anniversary of the open-access database of transcription factor binding profiles Open Access. NAR 2023) and the recently reported CellOracle program (Kamimoto et al. Dissecting cell identity via network inference and in silico gene perturbation. Nature 2023). Then, we performed downstream analyses and obtained two major results. One is that on average (per base), fewer selection signals are detected in HS TF DBSs (anyway, caution is needed because TF DBSs are very short); the other is that HS TFs and HS lncRNAs contribute to human evolution in quite different ways (Supplementary Figs. 25 and 26).

(3) On genes with more transcripts may appear as spurious targets of HS lncRNAs.

Now, the results of HS TF DBSs allow us to address the question of whether genes with more transcripts may appear as spurious targets of HS lncRNAs. We note that (a) we predicted HS lncRNA DBSs and HS TF DBSs in the same promoter regions before the same 179128 Ensembl-annotated transcripts (release 79), (b) we used the same GTEx transcript expression matrices in the analyses of HS TF DBSs and HS lncRNA DBSs (the GTEx database includes gene expression matrices and transcript expression matrices, the latter includes multiple transcripts of a gene). Thus, the analyses of HS TF DBSs provide an effective control for examining the question of whether genes with more transcripts may appear as spurious targets of HS lncRNAs, and consequently, cause the high percentages of HS lncRNA-target transcript pairs that show correlated expression in the brain (Figure 3). We find that the percentages of HS TF-target transcript pairs that show correlated expression are also high in the brain, but the whole profile in GTEx tissues is significantly different from that of HS lncRNA DBSs (Figure 3A; Supplementary Figure 25). On the other hand, on the distribution of significantly changed DBSs in GTEx tissues, the difference between HS lncRNA DBSs and HS TF DBSs is more apparent (Figure 3B; Supplementary Figure 26). Together, these suggest that the brain-enriched distribution of co-expressed HS lncRNA-target transcript pairs must arise from HS lncRNA-mediated transcriptional regulation rather than from the transcript number difference.

(4) Additional notes on HS TFs and HS TF DBSs.

First, the “many2zero” and “one2zero” gene lists in the “hg38-panTro6” dataset of Kirilenko et al. provide the most update, but not most complete, data on human-specific genes because “hg38-panTro6” is a pairwise comparison. On the other hand, the Ensembl database also annotates orthologous genes, but lacks such pairwise comparisons as “hg38-panTro6”. Therefore, not all HS genes based on “hg38-panTro6” agree with orthologous genes in the Ensembl database. Second, if HS genes are identified based on both Ensembl and Kirilenko et al., HS TFs will be fewer.

(5) On speculative or hyperbolic claims.

First, the title “Human-specific lncRNAs contributed critically to human evolution by distinctly regulating gene expression” is now further supported by HS TF DBSs analyses. Second, we have carefully revised the entire manuscript, trying to make it more readable, accurate, logically reasonable, and biologically acceptable. Third, specifically, in the revision, we avoid speculative or hyperbolic claims in results, interpretations, and discussions as possible as we can. This includes the tone-down of statements and claims, for example, using “reshape” to replace “rewire” and using “suggest” to replace “indicate”. Since the revisions are pervasive, we do not mark all of them, except those that are directly relevant to the reviewer’s comments.

(1) Line 155: "About 5% of genes have significant sequence differences in humans and chimpanzees," This statement needs a citation, and a definition of what is meant by 'significant', especially as multiple lines below instead mention how it's not clear how many differences matter, or which of them, etc.

Different studies give different estimates, from 1.24% (Ebersberger et al. Genomewide Comparison of DNA Sequences between Humans and Chimpanzees. Am J Hum Genet. 2002) to 5% (Britten RJ. Divergence between samples of chimpanzee and human DNA sequences is 5%, counting indels. PNAS 2002). The 5% for significant gene sequence differences arises when considering a broader range of genetic variations, particularly insertions and deletions of genetic material (indels). To provide more accurate information, we have replaced this simple statement with a more comprehensive one and cited the above two papers.

(2) line 187: "Notably, 97.81% of the 105141 strong DBSs have counterparts in chimpanzees, suggesting that these DBSs are similar to HARs in evolution and have undergone human-specific evolution." I do not see any support for the inference here. Identifying HARs and acceleration relies on a far more thorough methodology than what's being presented here. Even generously, pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee.

Here, we actually made an analogy but not an inference; therefore, we used such words as “suggesting” and “similar” instead of using more confirmatory words. We have revised the latter half sentence, saying “raising the possibility that these sequences have evolved considerably during human evolution”.

(3) line 210: "Based on a recent study that identified 5,984 genes differentially expressed between human-only and chimpanzee-only iPSC lines (Song et al., 2021), we estimated that the top 20% (4248) genes in chimpanzees may well characterize the human-chimpanzee differences". I do not agree with the rationale for this claim, and do not agree that it supports the cutoff of 0.034 used below. I also find that my previous concerns with the very disparate numbers of results across the three archaics have not been suitably addressed.

(1) Indeed, “we estimated that the top 20% (4248) genes in chimpanzees may well characterize the human-chimpanzee differences” is an improper claim; we made this mistake due to the flawed use of English.

(2) What we need is a gene number, which (a) indicates genes that effectively differentiate humans from chimpanzees, (b) can be used to set a DBS sequence distance cutoff. Since this study is the first to systematically examine DBSs in humans and chimpanzees, we must estimate this gene number based on studies that identify differentially expressed genes in humans and chimpanzees. We choose Song et al. 2021 (Song et al. Genetic studies of human–chimpanzee divergence using stem cell fusions. PNAS 2021), which identified 5984 differentially expressed genes, including 4377 genes whose differential expression is due to trans-acting differences between humans and chimpanzeees. To the best of our knowledge, this is the only published data on trans-acting differences between humans and chimpanzeees, and most HS lncRNAs and their DBSs/targets have trans-acting relationships (see Supplementary Table 2). Based on these numbers, we chose a DBS sequence distance cutoff of 0.034, which corresponds to 4248 genes (the top 20%), slightly fewer than 4377.

(3) If we chose DBS sequence distance cutoff=0.033 or 0.035, slightly more or fewer genes would be determined, raising the question of whether they would significantly influence the downstream gene set enrichment analysis (Figure 2). We found that 91 genes have a DBS sequence distance of 0.034. Thus, if cutoff=0.035, 4248-91=4157 genes were determined, and the influence on gene set enrichment analysis was very limited.

(4) On the disparate numbers of results across the three archaics. Figure 1A is based on Figure 2 in Prufer et al. 2017. At first glance, our Figure 1A indicates that Altai Neanderthal is older than Denisovan (upon kya), making our result “identified 1256, 2514, and 134 genes in Altai Neanderthals, Denisovans, and Vindija Neanderthals” unreasonable. However, Prufer et al. (2017) reported that “It has been suggested that Denisovans received gene flow from a hominin lineage that diverged prior to the common ancestor of modern humans, Neandertals, and Denisovans……In agreement with these studies, we find that the Denisovan genome carries fewer derived alleles that are fixed in Africans, and thus tend to be older, than the Altai Neandertal genome”. This note by Prufer et al. provides an explanation for our result, which is that more genes with large DBS sequence distances were identified in Denisovans than in Altai Neanderthals. Of course, the 1256, 2514, and 134 depend on the cutoff of 0.034. If cutoff=0.035, these numbers change slightly, but their relationships remain (i.e., more genes in Denisovans). We examined multiple cutoff values and found that more genes in Denisovans have large DBS sequence distances than in Altai Neanderthals.

(4) I also think that there is still too much of a tendency to assume that adaptive evolutionary change is the only driving force behind the observed results in the results. As I've stated before, I do not doubt that lncRNAs contribute in some way to evolutionary divergence between these species, as do other gene regulatory mechanisms; the manuscript leans down on it being the sole, or primary force, however, and that requires much stronger supporting evidence. Examples include, but are not limited to:

(1) Indeed, the observed results are also caused by other genomic elements and mechanisms (but it is hardly feasible to identify and differentiate them in a single study), and we do not assume that adaptive evolutionary change is the only driving force. Careful revisions have been made to avoid leaving readers the impression that we have this tendency or hold the simple assumption.

(2) Comparing HS lncRNAs to HS TFs is critical, and we have done this.

(5) line 230: "These results reveal when and how HS lncRNA-mediated epigenetic regulation influences human evolution." This statement is too speculative.

We have toned down the statement, just saying “These results provide valuable insights into when and how HS lncRNA-mediated epigenetic regulation impacts human evolution”.

Line 268: "yet the overall results agree well with features of human evolution." What does this mean? This section is too short and unclear.

(1) First, the sentence “Selection signals in YRI may be underestimated due to fewer samples and smaller sample sizes (than CEU and CHB), yet the overall results agree well with features of human evolution” has been deleted, because CEU, CHB, and YRI samples are comparable (100, 99, and 97, respectively).

(2) Now the sentence has been changed to “These results agree well with findings reported in previous studies, including that fewer selection signals are detected in YRI (Sabeti et al., 2007; Voight et al., 2006)”.

(3) On “This section is too short and unclear” - To make the manuscript more readable, we adopt short sections instead of long ones. This section expresses that (a) our finding that more selection signals were detected in CEU and CHB than in YRI agrees with well-established findings (Voight et al. A Map of Recent Positive Selection in the Human Genome. PLoS Biology 2006; Sabeti et al. Genome-wide detection and characterization of positive selection in human populations. Nature 2007), (b) in considerable DBSs, selection signals were detected by multiple tests.

Line 325: "and form 198876 HS lncRNA-DBS pairs with target transcripts in all tissues." This has not been shown in this paper - sequence based analyses simply identify the “potential” to form pairs.

This section describes transcriptomic analysis using the GTEx data. Indeed, target transcripts of HS lncRNAs are results of sequence-based analysis, and a predicted target is not necessarily regulated by the HS lncRNA in a tissue. Here, “pair” means a pair of HS lncRNA-target transcript whose expression shows significant Pearson correlation in a GTEx tissue (by the way, we do not mean correlation equals regulation; actually, we identified HS lncRNA-mediated transcriptional regulation upon both DBS-targeting relationship and correlation relationship).

Line 423: "Our analyses of these lncRNAs, DBSs, and target genes, including their evolution and interaction, indicate that HS lncRNAs have greatly promoted human evolution by distinctly rewiring gene expression." I do not agree that this conclusion is supported by the findings presented - this would require significant additional evidence in the form of orthogonal datasets.

(1) As mentioned above, we have used “reshape” to replace “rewire” and used “suggest” to replace “indicate”. In addition, we have substantially revised the Discussion, in which this sentence is replaced by “our results suggest that HS lncRNAs have greatly reshaped (or even rewired) gene expression in humans”.

(2) Multiple citations have been added, including Voight et al. 2006 (Voight et al. A Map of Recent Positive Selection in the Human Genome. PLoS Biology 2006) and Sabeti et al. 2007 (Sabeti et al. Genome-wide detection and characterization of positive selection in human populations. Nature 2007).

(3) We have analyzed HS TF DBSs, and the obtained results also support the critical contribution of HS lncRNAs.

I also return briefly to some of my comments before, in particular on the confounding effects of gene length and transcript/isoform number. In their rebuttal the authors argued that there was no need to control for this, but this does in fact matter. A gene with 10 transcripts that differ in the 5' end has 10 times as many chances of having a DBS than a gene with only 1 transcript, or a gene with 10 transcripts but a single annotated TSS. When the analyses are then performed at the gene level, without taking into account the number of transcripts, this could introduce a bias towards genes with more annotated isoforms. Similarly, line 246 focuses on genes with "SNP numbers in CEU, CHB, YRI are 5 times larger than the average." Is this controlled for length of the DBS? All else being equal a longer DBS will have more SNPs than a shorter one. It is therefore not surprising that the same genes that were highlighted above as having 'strong' DBS, where strength is impacted by length, show up here too.

(1) In gene set enrichment analysis (Figure 2, which is a gene-level analysis), when determining genes differentiating humans from chimpanzees based on DBS sequence distance, if a gene has multiple transcripts/DBSs, we choose the DBS with the largest distance. That is, the input to g:Profiler is a non-redundant gene list.

(2) In GTEx data analysis (Figure 3, which is a transcriptome-level analysis), the analyses of HS TF DBSs using the GTEx data provide evidence suggesting that different DBS/transcript numbers of genes are unlikely to cause confounding effects. As explained above, we predicted HS TF DBSs in the same promoter regions of 179128 Ensembl-annotated transcripts (release 79), but Supplementary Figures 25 and 26 are distinctly different from Figure 3AB.

(3) In evolutionary analysis, a gene with 10 DBSs has a higher chance of having selection signals than a gene with 1 DBS. This is biologically plausible, because many conserved genes have novel transcripts whose expression is species-, tissue-, or developmental period-specific, and DBSs before these novel transcripts may differ from DBSs before conserved transcripts.

(4) “line 246 focuses on genes with "SNP numbers in CEU, CHB, YRI are 5 times larger than the average." Is this controlled for the length of the DBS?” - This is a defect. We have now computed SNP numbers per base and used the new table to replace the old Supplementary Table 8. After examining the new table, we find that the major results of SNP analysis remain.

(5) On “Is this controlled for length of the DBS? All else being equal a longer DBS will have more SNPs than a shorter one” - We do not think there are reasons to control for the length of DBSs; also, what “All else being equal” means matters. First, DBS sequences have specific features; thus, the feature of a long DBS is stronger than the feature of a short one, making a long DBS less likely to be generated by chance in the genome and less likely to be predicted wrongly than a short one. This means that longer DBSs are less likely to be false ones (note our explanation that the chance of a DBS of 147 bp, the mean length of DBSs, to be wrongly predicted is extremely low, p<8.2e-19 to 1.5e-48). Second, the difference in length suggests a difference in binding affinity, which in turn influences the regulation of the specific transcripts and influences the analysis of GTEx data. Third, it cannot be excluded that some SNPs may be selection signals (detecting selection signal is challenging, and many selection signals cannot be detected by statistical tests, see Grossman et al. A composite of multiple signals distinguishes causal variants in regions of positive selection. Science 2010).

(6) On “It is therefore not surprising that the same genes that were highlighted above as having 'strong' DBS, where strength is impacted by length” - Indeed, strength is influenced by length, see the above response.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Finally, figure 1 panels D and F are not legible - the font is tiny! There's also a typo in panel A, where "Homo Sapien" should be "Homo sapiens".

(1) “Homo sapien” is changed to “Homo sapiens”.

(2) Even if we double the font size, they are still too small. Inserting a very large panel D into Figure 1 will make Figure 1 ugly, and converting Figure 1D into an independent figure is unnecessary. Actually, panels 1D and F are illustrative figures; the full Fig.1D is Supplementary Figure 6, and the full Fig.1F is Figure 3. We have revised Fig.1’s legend to explain these.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This unique study reports original and extensive behavioral data collected by the authors on 21 living mammal taxa in zoo conditions (primates, tree shrew, rodents, carnivorans, and marsupials) on how descent along a vertical substrate can be done effectively and securely using gait variables. Ten morphological variables reflecting head size and limb proportions are examined in relationship to vertical descent strategies and then applied to reconstruct modes of vertical descent in fossil mammals.

Strengths:

This is a broad and data-rich comparative study, which requires a good understanding of the mammal groups being compared and how they are interrelated, the kinematic variables that underlie the locomotion used by the animals during vertical descent, and the morphological variables that are associated with vertical descent styles. Thankfully, the study presents data in a cogent way with clear hypotheses at the beginning, followed by results and a discussion that addresses each of those hypotheses using the relevant behavioral and morphological variables, always keeping in mind the relationships of the mammal groups under investigation. As pointed out in the study, there is a clear phylogenetic signal associated with vertical descent style. Strepsirrhine primates much prefer descending tail first, platyrrhine primates descend sideways when given a choice, whereas all other mammals (with the exception of the raccoon) descend head first. Not surprisingly, all mammals descending a vertical substrate do so in a more deliberate way, by reducing speed, and by keeping the limbs in contact for a longer period (i.e., higher duty factors).

Weaknesses:

The different gait patterns used by mammals during vertical descent are a bit more difficult to interpret. It is somewhat paradoxical that asymmetrical gaits such as bounds, half bounds, and gallops are more common during descent since they are associated with higher speeds and lower duty factors. Also, the arguments about the limb support polygons provided by DSDC vs. LSDC gaits apply for horizontal substrates, but perhaps not as much for vertical substrates.

We analyzed gait patterns using methods commonly found in the literature and discussed our results accordingly. However, the study of limbs support polygons was indeed developed specifically for studying locomotion on horizontal supports, and may not be applicable for studying vertical locomotion, which is in fact a type of locomotion shared by all arboreal species. In the future, it would be interesting to consider new methods for analyzing vertical gaits.

The importance of body mass cannot be overemphasized as it affects all aspects of an animal's biology. In this case, larger mammals with larger heads avoid descending head-first. Variation in trunk/tail and limb proportions also covaries with different vertical descent strategies. For example, a lower intermembral index is associated with tail-first descent. That said, the authors are quick to acknowledge that the five lemur species of their sample are driving this correlation. There is a wide range of intermembral indices among primates, and this simple measure of forelimb over hindlimb has vital functional implications for locomotion: primates with relatively long hindlimbs tend to emphasize leaping, primates with more even limb proportions are typically pronograde quadrupeds, and primates with relatively long forelimbs tend to emphasize suspensory locomotion and brachiation. Equally important is the fact that the intermembral index has been shown to increase with body mass in many primate families as a way to keep functional equivalence for (ascending) climbing behavior (see Jungers, 1985). Therefore, the manner in which a primate descends a vertical substrate may just be a by-product of limb proportions that evolved for different locomotor purposes. Clearly, more vertical descent data within a wider array of primate intermembral indices would clarify these relationships. Similarly, vertical descent data for other primate groups with longer tails, such as arboreal cercopithecoids, and particularly atelines with very long and prehensile tails, should provide more insights into the relationship between longer tail length and tail-first descent observed in the five lemurs. The relatively longer hallux of lemurs correlates with tail-first descent, whereas the more evenly grasping autopods of platyrrhines allow for all four limbs to be used for sideways descent. In that context, the pygmy loris offers a striking contrast. Here is a small primate equipped with four pincer-like, highly grasping autopods and a tail reduced to a short stub. Interestingly, this primate is unique within the sample in showing the strongest preference for head-first descent, just like other non-primate mammals. Again, a wider sample of primates should go a long way in clarifying the morphological and behavioral relationships reported in this study.

We agree with this statement. In the future, we plan to study other species, particularly large-bodied ones with varied intermembral indexes.

Reconstruction of the ancient lifestyles, including preferred locomotor behaviors, is a formidable task that requires careful documentation of strong form-function relationships from extant species that can be used as analogs to infer behavior in extinct species. The fossil record offers challenges of its own, as complete and undistorted skulls and postcranial skeletons are rare occurrences. When more complete remains are available, the entire evidence should be considered to reconstruct the adaptive profile of a fossil species rather than a single ("magic") trait.

We completely agree with this, and we would like to emphasize that our intention here was simply to conduct a modest inference test, the purpose of which is to provide food for thought for future studies, and whose results should be considered in light of a comprehensive evolutionary model.

Reviewer #2 (Public review):

Summary:

This paper contains kinematic analyses of a large comparative sample of small to medium-sized arboreal mammals (n = 21 species) traveling on near-vertical arboreal supports of varying diameter. This data is paired with morphological measures from the extant sample to reconstruct potential behaviors in a selection of fossil euarchontaglires. This research is valuable to anyone working in mammal locomotion and primate evolution.

Strengths:

The experimental data collection methods align with best research practices in this field and are presented with enough detail to allow for reproducibility of the study as well as comparison with similar datasets. The four predictions in the introduction are well aligned with the design of the study to allow for hypothesis testing. Behaviors are well described and documented, and Figure 1 does an excellent job in conveying the variety of locomotor behaviors observed in this sample. I think the authors took an interesting and unique angle by considering the influence of encephalization quotient on descent and the experience of forward pitch in animals with very large heads.

Weaknesses:

The authors acknowledge the challenges that are inherent with working with captive animals in enclosures and how that might influence observed behaviors compared to these species' wild counterparts. The number of individuals per species in this sample is low; however, this is consistent with the majority of experimental papers in this area of research because of the difficulties in attaining larger sample sizes.

Yes, that is indeed the main cost/benefit trade-off with this type of study. Working with captive animals allows for large comparative studies, but there is a risk of variations in locomotor behavior among individuals in the natural environment, as well as few individuals per species in the dataset. That is why we plan and encourage colleagues to conduct studies in the natural environment to compare with these results. However, this type of study is very time-consuming and requires focusing on a single species at a time, which limits the comparative aspect.

Figure 2 is difficult to interpret because of the large amount of information it is trying to convey.

We agree that this figure is dense. One possible solution would be to combine species by phylogenetic groups to reduce the amount of information, as we did with Fig. 3 on the dataset relating to gaits. However, we believe that this would be unfortunate in the case of speed and duty factor because we would have to provide the complete figure in SI anyway, as the species-level information is valuable. We therefore prefer to keep this comprehensive figure here and we will enlarge the data points to improve their visibility, and provide the figure with a sufficiently high resolution to allow zooming in on the details.

Author response:

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

Reviewer #2 had several remaining suggestions:

In some instances, the authors face well-known limitations. For example, bath application of drugs. Blockers of Gly and Gaba receptors are likely problematic when studying a network that includes a diverse set of inhibitory interneurons. Likewise, the results derived from application of AMPAR and KAR blockers should impact HC cell fxn, and presumably inner retina interneuron networks. In the Discussion the authors are encouraged to address more of these concerns (e.g., Discussion line 709).

Rather than concluding that the bath application of drugs is without complications, they can conclude that under the experimental conditions, glutamate release from these On-bipolars continues to exhibit Transient and Sustained release. This is really the key point of their study.

This is a good suggestion.  We have added a discussion of the complications of the pharmacology starting on line 754.  

If indeed sustained release is a reflection of higher release rates, ribbon size is what point to but, there are many other possibilities, such as SV recycling, or recruitment of reserve pools of SVs, fusion machinery, Cav channel behavior. The authors could cite more literature in the Discussion.

We added a sentence to this effect in the discussion, starting on line 866.

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

Reviewer #1 (Public Review): 

Summary: 

In the retina, parallel processing of cone photoreceptor output under bright light conditions dissects critical features of our visual environment and is fundamental to visual function. Cone photoreceptor signals are sampled by several types of bipolar cells and passed onto the ganglion cells. At the output of retinal processing, retinal ganglion cells send about 40 different codes of the visual scene to the brain for further processing. In this study, the authors focus on whether subtype-specific differences in the size of synaptic ribbon-associated vesicle pools of bipolar cells contribute to different retinal ganglion cell (RGC) responses. Specifically, inputs to ON alpha RGCs producing transient versus sustained kinetics (ON-S vs. ON-T, respectively) are compared. The authors first demonstrate that ON-S vs. ON-T RGCs are readily identifiable in a whole mount preparation and respond differently to both static and to a spatially uniform, randomly fluctuating (Gaussian noise) light stimulus. Liner-nonlinear (LN) models were used to estimate the transformation between visual input and excitatory synaptic input for each RGCs; these models suggested the presence of transient versus sustained kinetics already in the excitatory inputs to ON-T and ON-S RGCs. Indeed, the authors show that (glutamatergic) excitatory inputs to ON-S vs. ON-T RGCs are of distinct kinetics. The subtypes of bipolar cells providing input to ON-S are known (i.e., type 6 and 7), but the source of excitatory bipolar inputs to ON-T RGCs needed to be determined. In a tedious process, it is elegantly shown here that ON-T RGCs receive most of their excitatory inputs from type 5 and 6 bipolars. Interestingly, the temporal properties of light-evoked responses of type 5, 6, and 7 bipolars recorded from the somas were indistinguishable and rather sustained, suggesting that the origin of transient kinetics of excitatory inputs to ON-T RGCs suggested by the LN model might be found in the processing of visual signals at the bipolar cell axon terminal. Blocking GABA- or glycinergic inhibitory inputs did not alter the light-evoked excitatory input kinetics to ON-T and ON-S RGCs. Twophoton glutamate sensor imaging revealed significantly faster kinetics of light-evoked glutamate signals at ON-T versus ON-S RGCs. Detailed EM analysis of bipolar cell ribbon synapses onto ON-T and ON-S RGCs revealed fewer ribbon-associated vesicles at ON-T synapses, which is consistent with stronger paired-flash depression of lightevoked excitatory currents in ON-T RGCS versus ON-S RGCs. This study suggests that bipolar subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to transient versus sustained kinetics in RGCs. 

Strengths: 

The use of multiple, state-of-the-art tools and approaches to address the kinetics of bipolar to ganglion cell synapse in an identified circuit. 

Weaknesses: 

For the most part, the data in the paper support the conclusions, and the authors were careful to try to address questions in multiple ways. Two-photon glutamate sensor imaging experiment showing that blocking GABA- and glycinergic inhibition does not change the kinetics of light-evoked glutamate signals at ON-T RGCs would strengthen the conclusion that bipolar subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to transient versus sustained kinetics in RGCs. 

Thank you for this suggestion. We have revised the text throughout to be careful not to imply that amacrine cells have no role in shaping EPSCs and spike output, but instead that the transience of the On-T responses persists without amacrine cells (see for example lines 91, 450-453, 514-518, 696-714). We have also added additional iGluSnFR experiments to the paper to further test this conclusion (new Figure 7). The new data shows that the transience of glutamate release from the On-T cells is retained when 1) spiking amacrine cell activity is suppressed by blocking voltage-gated Na⁺ channels with TTX or 2) all amacrine cell activity is suppressed by blocking AMPA receptors with NBQX. This does provide nice additional evidence that amacrine cells are not necessary for the sustained/transient distinction.

Reviewer #2 (Public Review): 

Summary: 

Goal of the study. The authors tried to pinpoint the origins of transient and sustained responses measured at retinal ganglion cells (rgcs), which is the output layer of the retina. Response characteristics of rgcs are used to group them into different types. The diversity of rgc types represents the ability of the retina to transform visual inputs into distinct output channels. They find that the physical dimensions of bipolar cell's synaptic ribbons (specialized release sites/active zones) vary across the different types of cone on-bpcs, in ways that they argue could facilitate transient or sustained release. This diversity of release output is what they argue underlies the differences in on-rgcs response characteristics, and ultimately represents a mechanism for creating parallel cone-driven channels. 

Strengths: 

The major strengths of the study are the anatomical approaches employed and the use of the "glutamate sniffer" to assay synaptic glutamate levels. The outline of the study is elegant and reflects the strengths of the authors. 

Weaknesses: 

The major weakness is that the ambitious outline is not matched with a complete set of results, and the set of physiological protocols is disjointed, not sufficient to bridge the systems-level question with the presynaptic release question. 

Thank you for this comment as it provides an opportunity (here and in the paper) for us to clarify our main goal. We wanted to link the well-established distinction between transient and sustained retinal responses to anatomy. This required locating where this difference arises within the circuitry – which we show to be at least largely the bipolar output synapse – and then examining the structure of this synapse in detail. While we would certainly be interested in connecting our results to a biophysical description of the synapse, that was not the primary focus of our study and was not something we could add without substantial additional work.  

Major comments on the results and suggestions. 

The ribbon model of release has been explored for decades and needs to be further adapted to systems-level work. The study under consideration by Kuo et al. takes on this task. Unfortunately, the experimental design does not permit a level of control over presynaptic/bpc behavior that is comparable to earlier studies, nor do they manipulate release in ways that test the ribbon model (i.e., paired recordings or Ribeye-ko). Furthermore, the data needs additional evaluation, and the presentation and interpretations should draw on published biophysical and molecular studies. 

As described above, our goal was to test several possible explanations for the difference between transient and sustained responses in OnT and OnS ganglion cells: (1) differences in the light responses of the bipolar cells that convey photoreceptor signals to the relevant ganglion cells; (2) shaping of bipolar transmitter release by presynaptic inhibition; (3) shaping of ganglion cell responses by postsynaptic inhibition or spike generation; (4) differences in feedforward bipolar synapses. We were surprised to find that the feedforward bipolar synapses play a central role in this difference, and your comment nicely prompts us to relate this to the large literature on biophysical studies of release from ribbon synapses. We have made substantial revisions in the text to do this. This includes anticipating the importance of feedforward synaptic properties in the abstract and introduction (lines 36-37 and 61-64), pointers in the results (lines 539-548), and several new paragraphs in the discussion (starting on lines 751, 773 and 787). By showing that the transient/sustained differences originates largely at feedforward bipolar synapses, we set the stage for future work that shows how biophysical properties of the synapse shape physiological signals that traverse it.

To build a ribbon-centric context, consider recent literature that supports the assertion that ribbons play a role in forming AZ release sites and facilitating exocytosis. Reference Ribeye-ko studies. For example, ribbonless bpcs show an 80% reduction in release (Maxeiner et al EMBO J 2016), the ribbonless retina exhibits signaling deficits at the output layer (Okawa et al ...Rieke, ..Wong Nat Comm 2019), and ribbonless rods show an 80% reduction the readily releasable pool (RRP) of SVs (Grabner Moser, elife 2021). In addition, the authors could refer to whole-cell membrane capacitance studies on mammalian rods, cones, and bpcs, because the size of the RRP of SVs scales with the dimensions and numbers of ribbons (total ribbon footprint). For comparison, bipolars see the review by Wan and Heidelberger 2011. For a comparison of mammalian rods and cones, see, rods: Grabner and Moser (2021 eLife), Mueller.. Regus Leidig et al. (2019; J Neurosci) and cones Grabner ...DeVries (Nat Comm 2023). A comparison of cell types shows that the extent of release is (1) proportional to the total size of the ribbon footprint, and (2) less release is witnessed when ribbons are deleted (also see photo ablation studies by Snellman.... And Mehta..Zenisek, Nat Neurosci and Neuron).

Thank you for these pointers into the literature.  We have included much of this work in the revised Discussion (see three paragraphs starting on line 751). The revised text focuses on the evidence that larger and more numerous ribbons lead to increased release. The direct evidence from previous work for this relationship supports our (indirect) conclusions in the current paper about the role of ribbon size and associated vesicle pools in transient vs sustained responses.  

Ribbon morphology may change in an activity-dependent manner. The rod ribbon AZ has been reported to lengthen in the dark (Dembla et al 2020), and deletion of the ribbon shortens the length of the AZ (defined by Cav1,4 or RIM2); in addition, the Ribeye-ko AZs fail to change in size with light and dark conditioning. Furthermore, EM studies on rod and cone AZs in light and dark argue that the number of SVs at the base of the ribbon increases in the dark, when PRs are depolarized (see Figure 10, Babai et al 2016 JNeurosci). Lastly, using goldfish Mb1 on-bipolars, Hull et al (2006, J Neurophysio) correlated an increase in release efficiency with an increase in ribbon numbers, which accompanied daylight. >> When release activity is high, ribbon AZ length increases (Dembla, rods), the number of docked SVs increases (Babai, rods cones), and the number of ribbons increases (Hull, diurnal Mb1s). 

We have extensively revised the discussion section to include more discussion of ribbons, particularly emphasizing evidence supporting the general argument that larger ribbons support higher release rates. We focused on studies that provided direct links between release rates and ribbon size or number of ribbon-associated vesicles.  This includes studies that pair electrophysiology and anatomy and those that measure the consequences of ablating ribbons,

The results under review, Kuo et al., were attained with SBF-SEM, which has the benefit of addressing large-volume questions as required here, yet it achieves lower spatial resolution than what is attained with TEM tomography and FIB-EM. Ideally, the EM description would include SV size, and the density of ribbon-tethered SVs that are docked at the plasma membrane, because this is where the SVs fuse (additional non-ribbon release sites may also exist? Mehta ... Singer 2014 J Neurosci). Studies by Graydon et al 2011 and 2014 (both in J Neurosci), and Jean ... Moser et al 2018 (eLife) are good examples of quantitative estimates of SVs docking sites at ribbons. SBF-SEM does not allow for an assessment of SVs within 5 nm of the PM, but if the authors can identify the number of SVs that appear within the limit of resolution (10 to 15 nm) from the PM, then this data would be useful. Also, what dimension(s) of the large ribbons make them larger? Typically, ribbons are fixed in height (at least in the outer retina, 200 to 250 nm), but their length varies and the number ribbons per terminal varies. Is the larger ribbon size observed in type 6 bpcs do to longer ribbons, or taller ribbons? A longer ribbon likely has more docked SVs. An additional possibility is that more SVs are about the ribbon-PM footprint, either more densely packed and/or expanding laterally (see definitions in Jean....Moser, elife 2018). 

We have included an additional analysis of ribbon surface area from our 3D SBFSEM reconstructions. As with the volume measurements included in the original submission, ribbon surface areas are distinct between type 5i and type 6 bipolar cells (Fig. S10A), ON-T RGCs on average receive input from ribbons with smaller surface area than ON-S RGCs (Fig. S10B), and ribbon surface area predicts the number of adjacent vesicles across bipolar cell types (Fig. S10C).  We agree that a higher resolution view of presynaptic structures would be very helpful, but the resolution of our SBF-SEM data is limited (e.g. each pixel is 40 nm on a side).  This resolution does not allow us to distinguish between vesicles at vs near the membrane. 

In our observations, both length and height of the ribbons showed variability across individual bipolar cells. And ribbons in type 6 bipolar cells tended to be either longer and/or taller compared to those in type 5 cells. We agree that a longer ribbon may accommodate more docked SVs. A more definitive analysis would benefit from higher-resolution, isotropic 3D reconstructions of ribbons, which would allow more precise shape analysis and ,together with a detailed assessment of docked SVs at the ribbons.

The ribbon literature given above makes the argument that ribbons increase exocytotic output, and morphological studies suggest that release activity enhances 1) ribbon length (Dembla) and 2) the density of SVs near the PM (Babai). These findings could lead one to propose that type 6 bpcs (inputs to On-sustained) are more active than type 5i (feed into On-transient). Here Kuo et al. show that the bpcs have similar Vm (measured from the soma) in response to light stimulation. Does Vm predict release? Not entirely as the authors acknowledge, because: Cav channel properties, SV availability, and negative feedback are all downstream of bpc Vm. The only experiment performed to test downstream factors focused on negative feedback from amacrines. The data presented in Figures 5C-F led me to conclude the opposite of what the authors concluded. My impression is that the T-ON rgc exhibits strong disinhibition when GABA-blockers are applied (the initial phase is greatly increased in amplitude and broadened with the drug), which contrasts with the S-On rgc responses that show a change in the amplitude of the initial phase but not its width (taus would be nice). Here and in many places the authors refer to changes in release kinetics, without implementing a useful description of kinetics. For instance, take the cumulative current (charge) in Figure 5C and fit the control and drug traces to arrive at taus, and their respective amplitudes, and use these values to describe kinetic phases. One final point, the summary in Figure 5D has a p: 0.06, very close to the cutoff for significance, which begs for more than an n = 5. Given that previous studies have shown that bpc output is shaped by immediate msec GABA feedback, in ways that influence kinetic phases of release (..Mb1 bipolars, see Vigh et al 2005 Neuron), more attention to this matter is needed before the authors rule out feedback inhibition in favor of ribbon size. If by chance, type 5i bpcs are under uniquely strong feedback inhibition, then ribbon size may result from less activity, not less output resulting from smaller ribbons.

The text surrounding Figure 5 led to some confusion, and we have revised that text and the figure for clarity.  First, the data in that figure is entirely from On-T cells (the upper and lower panels show block of GABA and glycine receptors separately).  Second, the observation that we make there is that block of inhibitory receptors increases the transience of the On-T excitatory input, rather than decreasing it as would be expected if the transience is created by presynaptic inhibition. We have added additional data and that increase in transience is now significant. Inhibitory block does substantially increase the amplitude of the postsynaptic response, and a likely origin of this change in response is inhibitory feedback to the bipolar synaptic terminal. We now indicate this in the text on page 13, lines 438-453. 

The key result of this figure for our purposes here is that the transience of the excitatory input to the OffT cell remains with inhibitory input blocked. We have clarified throughout the text that our results indicate that inhibitory feedback is not necessary for the difference between transient release into On-T and sustained release onto On-S. This does not mean that inhibitory feedback does not shape the responses in other ways or contribute to the transient/sustained difference - just that for the specific stimuli we use that difference is retained without presynaptic inhibition. We have also added citations to past work showing that activity of amacrine cells can modulate bipolar transmitter release. 

Whether strong feedback inhibition limits activity and therefore limits ribbon size in an activity-dependent way is an intriguing possibility. Indeed, addressing why ribbons are larger in type 6 bipolar cells vs. other bipolar types will be an interesting avenue of further study. However, it would be surprising if ribbon sizes changed during the acute pharmacological block conditions (~10-15 minutes) we employed in our study. Our point here is that there is an interesting correlation between presynaptic ribbon size and the kinetics of glutamate release. We do not think that the two possibilities stated in the last sentence (“…ribbon size may result from less activity, not less output resulting from smaller ribbons”) are mutually exclusive.

We have not further quantified the response kinetics in the experiments of Figure 5 as the large changes induced by the pharmacology (especially GABA receptor block) make it unclear how to interpret quantitative differences.  In other places we have quantified kinetics through the STA or specified that our focus was more qualitative (i.e. transient vs sustained kinetics). 

As mentioned above, the behavior of Cav channels is important here. This is difficult to address with voltage clamps from the soma, especially in the Vm range relevant to this study. Given that it has previously been modeled that the rod bpc to AII pathway adapts to prolonged depolarization of rbcs through downregulating Cav channel-mediated Ca²⁺ influx (Grimes ....Rieke 2014 Neuron), it seems important for Kou et al to test if there is a difference in Cav regulation between type 6 and 5i bpcs. Ca²⁺  imaging with a GCaMP strategy (Baden....Lagnado Current Biology, 2011) or filling the presynapse with Ca dyes (see inner hair cells: Ozcete and Moser, EMBO J 2020) would allow for the correlation of [Ca]intra with GluSnf signals (both local readouts).

This is a good suggestion but is outside the scope of our current paper. Our focus was on the circuit origin of the difference in response of the OnT and OnS responses rather than the specific biophysical mechanism.  We are of course interested in the mechanism, but the additional experiments needed to pin that down would need to be a part of future experiments. The work here represents an important step in that direction as it greatly reduces the number of possible locations and mechanisms for the sustained/transient difference and hence serves to focus any future mechanistic investigations.

Stimulation protocol and presentation of Glutamate Sniffer data in Figure 6. In all of your figures where you state steady st as a % of pk amplitude, please indicate in the figure where you estimate steady state. Alternatively, if you take the cumulative dF/F signal, then you can fit the different kinetic phases. From the appearance of the data, the Sustained Glu signals look like square waves (Figure 6B ROI1-4), without a transient at onset, which is not predicted in your ribbon model that assumes different kinetic phases (1. depletion of docked SVs, and 2. refilling and repriming). The Transient responses (Figure 6B ROI5-8) are transient and more compatible with a depressing ribbon scheme. If you take the cumulative, for all of the On-S and compare it to all of the On-T responses, my guess is the cumulative dF/F will be 10 to 20 larger for the S-On. Would you conclude that bpc inputs to On-S (type 6) release 20fold more SVs per 4 seconds on a per ribbon basis, and does the surface area of the type 6 bpcs account for this difference? From Figures 8B and D, the volume of the ribbon is ~2 fold greater for type 6 vs 5i, but the Surface Area (both faces of ribbon) is more relevant to your model that claims ribbon size is the pivotal factor. If making cumulative traces, and comparisons on an absolute scale is unfounded, then we need to know how to compare different observations. The classic ribbon models always have a conversion factor such as the capacitance of an SV or q size that is used to derive SV numbers from total dCm or Qcontent. See Kim ....et al von Gersdorff, 2023, Cell Reports. Why not use the Gaussian noise stimulus in Fig 6 as in Figure 1 and 2? 

For iGluSnFR recordings, steady-state responses were measured from the mean fluorescence over the last 1 sec of the light step (2 sec duration) response. We have included this information in the figure caption and in the Methods. 

There is a good deal of variability in the iGluSnR responses from one ROI to another, and the ROIs shown in the original submission had a less prominent transient component than many other ROIs. We have replaced this figure with another that is more representative of the average behavior across ROIs. The full range of behavior is captured in Figure 6C; it is clear across ROIs that glutamate release near ON-S dendrites shows both sustained and transient components. The new experiments in which we block amacrine cell activity also include a few more example ROIs from ON-S cells, and those also show both transient and sustained components.

Your suggestion to integrate the iGluSnFR signals to compare to our structural analysis of ribbons is interesting. However, we are hesitant to make a quantitative comparison between the two without further experiments to validate how the iGluSnFR signals we measure relate to release of single vesicles. For example, a quantitative measure of release based on the iGluSnR experiments would require accounting for possible differences in the expression of the indicator - which could differ both in overall level and/or location relative to release sites. 

This comment and one above highlight the importance of measures of ribbon surface area, which we now provide (Figure S10).

Figure 7. What is the recovery time for mammalian cones derived from ribbon-based models? There are estimates from membrane capacitance studies. Ground squirrel cones take 0.7 to 1 sec to recover the ultrafast, primed pool of SVs when probed with a paired-pulse protocol (Grabner ...DeVries 2016, Neuron). Their off-bpcs take anywhere from under 0.2 sec to a second to recover, which is a combination of many synaptic factors (Grabner ...DeVries Nat Comm 2023). Rod On bpcs take over a second (Singer Diamond 2006, reviewed Wan and Heidelberger 2011). In Figure 7B, the recovery time is ~150 ms for the responses measured at rgcs. This brief recovery time is incompatible with existing ribbon models of release. Whole-cell membrane capacitance measurements would be helpful here.

Thanks for drawing our attention to this issue. Indeed, we see a relatively rapid recovery in the paired-flash experiments. We now discuss this recovery time in the context of past measurements of recovery of responses in cones and bipolar cells (paragraph starting on line 773). There are many factors that could contribute to the relatively rapid recovery we observe - including synaptic factors such as those highlighted by Grabner et al., (2016) either at the cone-to-bipolar synapses or the bipolar-to-RGC synapses. We are certainly interested in a more detailed understanding of this issue, but the additional experiments are outside the scope of this paper.  

Experimental Suggestion: Add GABA blockers and see if type 5i bpc responds with more release (GluSniff) and prolonged [Ca2+] intra (GCaMP). Compare this to type 6 bpc behavior with GABA/gly blockers. This will rule in or out whether feedback inhibition is involved. 

Figure 7 in the revised manuscript includes two new experiments examining glutamate release (without the simultaneous measurement of bipolar cell intracellular calcium) while blocking (1) all/most amacrine cell-mediated inhibition via inclusion of NBQX in the bath solution, and (2) blocking spiking amacrine cells via inclusion of TTX in the bath solution. The transient vs sustained difference in light-evoked glutamate release around ON-T and ON-S RGC dendrites remained with amacrine activity suppressed. These new results are consistent with the anatomical and pharmacological data that were included in the initial submission of the manuscript (Fig. 5) that indicate presynaptic inhibition does not have a major role in shaping release kinetics at these synapses. 

Reviewer #3 (Public Review): 

Summary: 

Different types of retinal ganglion cell (RGC) have different temporal properties - most prominently a distinction between sustained vs. transient responses to contrast. This has been well established in multiple species, including mice. In general, RGCs with dendrites that stratify close to the ganglion cell layer (GCL) are sustained; whereas those that stratify near the middle of the inner plexiform layer (IPL) are transient. This difference in RGC spiking responses aligns with similar differences in excitatory synaptic currents as well as with differences in glutamate release in the respective layers - shown previously and here, with a glutamate sensor (iGluSnFR) expressed in the RGCs of interest. Differences in glutamate release were not explained by differences in the distinct presynaptic bipolar cells' voltage responses, which were quite similar to one another. Rather, the difference in transient vs. sustained responses seems to emerge at the bipolar cell axon terminals in the form of glutamate release. This difference in the temporal pattern of glutamate release was correlated with differences in the size of synaptic ribbons (larger in the bipolar cells with more sustained responses), which also correlated with a greater number of vesicles in the vicinity of the larger ribbons. 

The main conclusion of the study relates to a correlation (because it is difficult to manipulate ribbon size or vesicle density experimentally): the bipolar cells with increased ribbon size/vesicle number would have a greater possibility of sustained release, which would be reflected in the postsynaptic RGC synaptic currents and RGC firing rates. This model proposes a mechanism for temporal channels that is independent of synaptic inhibition. Indeed, some experiments in the paper suggest that inhibition cannot explain the transient nature of glutamate release onto one of the RGC types. Still, it is surprising that such a diverse set of inhibitory interneurons in the retina would not play some role in diversifying the temporal properties of RGC responses. 

Strengths: 

(1) The study uses a systematic approach to evaluating temporal properties of retinal ganglion cell (RGC) spiking outputs, excitatory synaptic inputs, presynaptic voltage responses, and presynaptic glutamate release. The combination of these experiments demonstrates an important step in the conversion from voltage to glutamate release in shaping response dynamics in RGCs. 

(2) The study uses a combination of electrophysiology, two-photon imaging, and scanning block-face EM to build a quantitative and coherent story about specific retinal circuits and their functional properties. 

Weaknesses: 

(1) There were some interesting aspects of the study that were not completely resolved, and resolving some of these issues may go beyond the current study. For example, it was interesting that different extracellular media (Ames medium vs. ACSF) generated different degrees of transient vs. sustained responses in RGCs, but it was unclear how these media might have impacted ion channels at different levels of the circuit that could explain the effects on temporal tuning.

We do not have an explanation for the quantitative differences in response kinetics we observed in Ames’ medium vs. ACSF. There are modest differences in calcium and magnesium concentration and a larger difference in potassium (2.5 mM in ACSF vs 3.6 mM in Ames). It would be interesting to test which of these (or other) differences accounts for the difference in response kinetics.

(2) It was surprising that inhibition played such a small role in generating temporal tuning. At the same time, there were some gaps in the investigation of inhibition (e.g., IPSCs were not measured in either of the RGC types; pharmacology was used to investigate responses only in the transient RGCs).

We were also surprised at this result. We have included additional data on inhibition in the revised manuscript. Figure S3 shows light-evoked IPSC data from both RGC types (Fig. S3) and Fig. 7 shows additional iGluSnFR measurements around both ON-T and ON-S RGC dendrites with inhibition blocked via bath application of NBQX (Fig. 7) and separately with inhibition from spiking amacrine cells blocked with TTX. These experiments provide additional evidence for the small role of inhibition. We attempted to measure the kinetics of excitatory input to ON-S cells with inhibition blocked, but we found that the excitatory input showed strong spontaneous oscillations under these conditions and the light responses were changed so drastically that we did not feel we could make a clear comparison with control conditions.

(3) There could be additional discussion and references to the literature describing several topics, including: temporal dynamics of glutamate release at different levels of the IPL; previous evidence that release sites from a single presynaptic neuron can differ in their temporal properties depending on the postsynaptic target; previous investigations of the role of inhibition in temporal tuning within retinal circuitry. 

Thanks, we have included more discussion and references to the relevant literature as you have suggested in the recommendations to authors.

Reviewer #1 (Recommendations For The Authors): 

The presented raw data of the pharmacological experiments show that SR95531 and TPMPA robustly increased both the amplitude and duration of the transient component of the light step-evoked excitatory currents, with slight, if any enhancement of the sustained component in ON-T RGCs Figure 5C. Statistical analysis of the population data (n=5) with Wilcoxon signed rank test yielded no significant difference (ln 363). However, reanalyzing the data extracted from the graph (Figure 5D) revealed that the difference between the paired observations is normally distributed (Shapiro-Wilk normality test, P=0.48) allowing parametric statistics to be used, which provides higher statistical power. Accordingly, reanalyzing the presented data with paired Student's t-test data revealed significant differences (P=0.01) in the steady-state amplitude normalized to that of the peak, recorded in the presence of SR95531 and TPMPA. In other words, based on the (rough) analysis of the presented pharmacology data GABAergic feedback inhibition significantly contributes to shaping the transient portion of the light-evoked excitatory currents in ON-T RGCs, by making it more transient. I believe a similar analysis based on the actual data is necessary, and the results should be communicated either way. However, if warranted, two-photon glutamate sensor imaging experiments showing that blocking GABA- and glycinergic inhibition does not change the kinetics of light-evoked glutamate signals at ON-T RGCs should also be performed, as these would be critical in drawing a conclusion regarding the effect of feedback inhibition on glutamate release from bipolar cells.

Thanks for this feedback. We have added another cell to the data set in Fig. 5D. With this addition, SR95531/TPMPA application significantly increases the response transience of excitatory currents measured in ON-T RGCs compared to control. This enhanced transience in GABA_A/C receptor blockers is due to an increase in the amplitude of the initial peak component of the response (control peak amplitude: -833.7±103.3 pA; SR95531+TPMPA peak amplitude: 2023±372.7pA; p=0.03, Wilcoxon signed rank test), with no change to the later sustained component (control plateau amplitude: -200.7±14.71pA; SR95531+TPMPA plateau amplitude: -290.9±43.69pA; p=0.15, Wilcoxon signed rank test).

We should clarify that this result indicates that GABAergic inhibition makes the excitatory inputs to ON-T RGCs less transient. Block of GABA receptors increased transience, thus intact GABAergic transmission appears to limit the initial peak of the response and therefore make excitatory currents more sustained. We unfortunately were not able to examine whether sustained excitatory currents in ON-S RGCs would become more transient using the same approach. In our hands, bath application of SR95531+TPMPA led to the generation of large-amplitude (>1nA) oscillatory bursts of excitatory input that developed within 5 minutes and persisted for the duration of the incubation (up to ~30 min) in drugs. Further, presentation of light steps tended to induce variable amplitude responses, likely dependent on the presence of spontaneous bursts; when large amplitude responses were evoked, these typically oscillated for several seconds after the step.

To examine a potential role for presynaptic inhibition in transient vs. sustained bipolar cell output, we therefore chose to eliminate amacrine cell-mediated inhibition by bath application of the AMPA/kainate receptor antagonist NBQX in additional iGluSnFR measurements. This manipulation should leave ON bipolar cell responses intact while eliminating most amacrine cell-mediated responses (and OFF bipolar cell driven responses). In separate experiments, we also eliminated inhibition from spiking amacrine cells by bath application of TTX. As shown in new Fig. 7, sustained and transient responses persisted in distal versus proximal RGC dendrites, respectively. Compared to SR95531/TPMPA, bath application of NBQX was not associated with spontaneous bursts of glutamate release around ON-S dendrites. These results show that amacrine cell-mediated inhibition is not required for either sustained or transient glutamate release from bipolar cells that provide input to ON-S and ON-T RGCs.

Small points: 

(1) The legend of Figure 1 (D) refers to shaded areas to show {plus minus} SEM, but no shade is visible (at least in my printout).

The SEM shading is there in Fig. 1D but is mostly obscured by the mean lines for the respective RGC types. We have added this to the figure caption.

(2) I found the reported Vrest for the ON bipolar cells somewhat depolarized. Perhaps due to the uncompensated junction potentials? 

These measurements are indeed not corrected for the liquid junction potential (which is approximately -10.8 mV between K-gluconate internal and Ames’ solution). We did not apply this correction since the appropriate value is not clear in perforated patch recordings as the intracellular chloride concentration is unknown (and can differ from that in the pipette solution). We have clarified this in the results text where we describe the Vrest values (lines 335-338).

(3) It is Wilcoxon signed rank test, not Wilcoxan. 

Thanks for catching this. This has been corrected in the revised manuscript.

Reviewer #2 (Recommendations For The Authors): 

Some amacrines express vesicular Glut-3 transporter and are reported to release glutamate (Marshak, Vis Neurosci 2016). Are Amacrine vGlut3 signals postsynaptic (within ~0.5 um) to cone bpc ribbons?

We did not characterize VgluT3-expressing amacrine cells in our SEM datasets. A recent study by Friedrichson et al. (Nat. Comm. 2024; PMID 38580652) using 3D SEM reconstructions found that Vglut3-amacrines are postsynaptic to both type 5i and type 6 bipolar cells, as well as other type 5/xbc bipolar cells (and receive >50% of their input from type 3a OFF bipolar cells).

How far apart are the postsynaptic targets from the ribbon release sites? The ribbons at type 5i bpc/On-T input appear separated from the dendrites of On-T rgcs (Figure 8C). At least further away than the type 6 bpc ribbons are from On-S rgc dendrites (Figure 8C). Distance may create a thresholding phenomenon, whereby only multivesicular bouts at the onset of depolarization are able to elevate synaptic Glu to levels needed to activate On-T GluRs. See Grabner et al Nat Comm 2023 for such scenarios in the outer retina.

This is an intriguing possibility, but we should point out that the presynaptic ribbons in Fig. 9C (former Fig. 8C) are similar distances (within the resolution of our reconstructions) from the ON-T and ON-S dendrites. We have increased the brightness of the dendrite segments for both RGC types in the resubmission figure; note that ON-T RGCs have spine-like protrusions that may not have been as apparent in the previously submitted version of our manuscript.

In Figures 1 and 2, Sustained responses look like the derivative of Transient responses, minus the negative going inflection. In addition, the sustained responses appear to have a lower threshold of activation than the transient On rgcs, because there are more bouts of action potentials (and membrane depol in V-clamp) with earlier onset in sustained than transients traces. It would be great if the GLuSniff data captured these differences. Take cumulative dF/F and see what the onset time is, or an initial tau if possible.

This is a good suggestion. However, we are reluctant to make detailed quantitative comparisons such as this without further validation of how the kinetics of the iGluSnFR signals relate to kinetics of glutamate release.  A specific concern is that differences in the location and amount of iGluSnFR expression could impact any such comparisons.

A recent study by Kim et al von Gersdorff (Cell Reports, 2023) presents interesting phases of release in response to light flashes, measured from AIIs, and complementary results from pairs of rbcs-AIIs. The findings highlight the complexity of SV pools under well-controlled experiments. Could their results be explained as variations in rbc ribbon size through development, and possibly between rbcs or within an rbc? 

This certainly seems possible and would be consistent with the dependence of release on ribbon size that our results support.  It would be interesting to see if there are clear anatomical correlates of that change in release properties.  

Figure 5 is a pivotal point in the study, but my review has identified numerous weaknesses. The feedback inhibition onto bipolar cell terminals is likely to sculpt glutamate release, and the results do not convincingly rule out this possibility. The suggestions for improvements range from the data needing to be reanalyzed with regard to statistical tests, and/or adding a few more data points (n = 5) before concluding a p: 0.06 is insignificant. 

We have added an additional recording to this data set. With n= 6 cells, there is now a statistically significant difference between ON-T RGC excitatory currents measured in control conditions versus during GABA_A/C receptor blockade. Please note that all the recordings shown in Figure 5C-F are from ON-T RGCs (the two panels show separately block of GABergic and glycinergic receptors). We did not make it sufficiently clear that the original trend (now statistically significant) is opposite of that expected if presynaptic GABAergic inhibition contributes to response transience in ON-T RGCs.  What we see is that excitatory synaptic inputs to ON-T RGCs become more transient (rather than mpre sustained) during GABA_A/C receptor blockade. We have revised the text in that section to make this point more clearly.

We have also included new data from iGluSnFR measurements showing that bath application of NBQX does not affect light step-evoked glutamate release kinetics at proximal (sustained) or distal (transient) RGC dendrites (control: steady-state amp. as % of peak amp. 13 ± 10; mean ± S.D.; n = 189 ROIs/4 FOVs for ON-T dendrites vs 40 ± 12; mean ± S.D.; n = 287 ROIs/8 FOVs for ON-S dendrites; NBQX: 6 ± 3; mean ± S.D.; n = 112 ROIs/1 FOV for ON-T dendrites vs 23 ± 9; mean ± S.D.; n = 97 ROIs/2 FOVs for ON-S dendrites; *p<0.001). By blocking glutamate receptors on amacrine cells, NBQX (AMPA/KAR antagonist) eliminates all/most amacrine cell-mediated signaling in the retina and should therefore abolish presynaptic inhibitory input to bipolar cell terminals across the IPL. Taken together, our results indicate that presynaptic inhibition does not play a critical role in establishing transient versus sustained kinetics for the stimulus conditions we employed in our study.

There is a need to cite more recent literature on bipolar cell ribbons (e.g. see Wakeham et al., Front. Cell. Neurosci., 2023), in order to support experimental design and interpretation of the results. The authors should discuss their Ribeye-KO data from Okawa et al 2019 Nat Comm, Figure 7, in the context of their new iGluSnFR results. 

Thank you for prompting us on this issue. We have expanded the discussion regarding ribbons and included more citations to the ribbon literature. That is largely in the three paragraphs starting on line 727.

One point deserves emphasis because it is central to the authors' ribbon model but not consistent with their data. The ribbon model as they put it, and as commonly stated, holds that a transient phase of release at the onset of depolarization indicates the depletion of the primed SVs, and the subsequent slower rate of release (steady state release in the authors' terms) reflects recruiting, priming, and release of new SVs. The On-transient dendrite GluSnf responses agree with this multiphasic process, but the sustained responses show only an elevation in glutamate without a pronounced initial peak, creating a square-wave-shaped response (Figure 6B). This does not agree with the simple ribbon-based release model. I would expect the signals from the T- and S-on dendrites to have a comparable initial phase, while the sustained phase should be greater in amplitude for the S-on dendrites. More discussion may clarify possible mechanisms.

Thanks for pointing this out. The example iGluSnFR traces we originally included in the manuscript were not entirely representative in that they did not show much initial transient phase. Note there is a distribution of steady-state amplitudes for proximal dendrites in Fig. 6C; the examples are from ROIs from the upper end of the distribution. In the new Figure 7, we have included some additional examples that show both a clear transient and sustained component. The summary data in Figure 6C shows the distribution of sustained/transient ratios across ROIs.  

Reviewer #3 (Recommendations For The Authors): 

(1) It would be interesting to understand the differences in IPSCs in the two RGC types. Perhaps they are small in both types, which would explain their apparent lack of impact on temporal tuning. The authors may already have these data.

We did make measurements of noise-evoked IPSCs (as well as EPSCs) in a subset of ON-T and ON-S recordings. We have now included this data as Figure S3. There are slight differences in the kinetics of inhibition between RGC types (Fig. S3C) and there is a trend towards stronger inhibition (relative to excitation) in ON-T RGCs compared to ON-S RGCs (Fig. S3E), although there is not a statistically significant difference. In both cases excitatory synaptic currents are as large or larger than inhibitory currents, and this does not include the difference in driving force near spike threshold which will favor excitatory input by a factor of 2-3.  Hence our data suggests that postsynaptic inhibition does not play a major role in generating the differential temporal spiking responses of ON-T and ON-S RGCs. However, additional experiments examining the relative contribution of excitation and inhibition to spiking output in these RGCs would be needed to reach a firm conclusion.

The pharmacological experiments in which we blocked inhibition (Fig. 5C-F, new Fig. 7) were designed to test the effect of presynaptic inhibition on bipolar cell output (voltage-clamp isolation of excitatory currents in Fig. 5; iGluSnFR measurements of glutamate release in Fig. 7). We do not mean to suggest that postsynaptic inhibition does not have any role in shaping the spiking behavior of these RGC types, but that transient vs. sustained kinetics are already present in the bipolar cell output and that presynaptic inhibition of bipolar cell terminals does not appear to account for this difference.  We have revised the text throughout to be clearer on this point.

(2) It could be convincing to show transient/sustained differences between RGC types in dim light, where the response would depend on the rod bipolar/AII circuit. In this case, any difference in temporal properties would presumably be explained by differences that localize to the cone bipolar cell axon terminals. Indeed, is that the result in Figure 1B? This seems to be a dim stimulus presented on darkness, which may be driven through the rod bipolar pathway. The authors could then discuss the interpretation of this data in terms of the rod bipolar circuit. 

Yes, Figure 1B is a dim light step (~30R*/rod/s) presented from darkness and the distinction between cells is clear down at still lower light levels that more effectively isolate signaling through the rod bipolar pathway. Thanks for making this point that observation of distinct temporal responses under scotopic conditions where signals suggests these differences must arise at and/or downstream of cone bipolar cell output. We have included additional text (lines 361-365) in the results describing bipolar cell responses that raise this point.

(3) Glutamate release was already measured across the full IPL depth by Borghuis et al. (2013) and Franke et al. (2017). It would be appropriate to better motivate the current study based on these existing measurements.

We have clarified that these important studies provided important motivation for measuring excitatory synaptic input to ON-T vs. ON-S RGCs (lines 165-169).   

(4) Line 212/213. It would be appropriate to add to the list of papers showing the different stratification of transient vs. sustained responses: Borghuis et al. (2013) and Beaudoin et al. (2019).

Thank you - these references have been added.  

(5) Line 635-638. It would be useful to discuss papers by Pottackal et al. (2020, 2021), which suggested that a single presynaptic cell (starburst) can signal with different temporal properties depending on the postsynaptic target (other starburst vs. DSGCs). The mechanism was not completely resolved (i.e., it was not explained by differences in presynaptic Ca channels at the two synapse types), but it at least shows that neurotransmitter release can show different filtering depending on the postsynaptic target from the same presynaptic neuron. (This could also be at play for the type 6 bipolar cell inputs to ON-S vs. ON-T RGCs in the present study.)

We have added a reference to Pottackal et al 2021 in this section.

(6) Line 714. Should describe the procedure for embedding the tissue in agarose. 

We have added more detail regarding agarose embedding for preparation of retinal slices in the methods.

(7) Line 775. Need a better description of the virus (not the construct), what serotype? Provide the Addgene number if available. 

This has been added to the methods.

(8) Line 808. Was the SD for the gaussian really 50%? That would cut off a lot of the distribution, i.e., it would get clipped at 0. 

Yes, the SD for Gaussian noise was 50%. This high contrast stimulus was used in part to achieve measurable signals from bipolar cells. You are correct that some of the distribution was clipped at 0 (it was also clipped at twice the mean to make sure that the distribution remained symmetrical). The clipping was accounted for during our LN analyses.

(9) The paper should discuss Swygart et al. (2024) results showing different spatial surround properties of neighboring synapses from a type 6 bipolar cell. Based on this result, it would seem very likely that amacrine cells could play a role in shaping the temporal processing of bipolar cell glutamate release as well. Indeed, spatial and temporal processing will not be completely independent in a typical experiment. For example, with the spot stimulus used in the present study, bipolar cells within the center versus the edge of the spot will have different balances of center/surround activation, which could potentially influence their temporal processing.

We have included discussion of results from Swygart et al 2024 in the section of the Discussion in which we point out differences in surround inhibition between ON-S and ON-T RGCs (lines 710-714). We agree that spatial and temporal processing are not completely independent. Our results with SR95531/TPMPA indicate ON-T RGCs receive stronger GABAergic surround inhibition than ON-S RGCs (Fig. S8). However, our results in Fig. 5C-D show GABAergic surround inhibition makes ON-T excitation more sustained rather than more transient. So even though bipolar cells presynaptic to ON-T RGCs receive stronger surround inhibition (Fig. S8), this inhibition does not establish the transient kinetics of glutamate release from these bipolar cells (in fact, it works to make release more sustained). Additional iGluSnFR experiments where we used NBQX to block all/most amacrine cell-mediated responses also suggest presynaptic inhibition does not have an important role in establishing differential glutamate release kinetics onto ON-S vs. ON-T RGC dendrites (Fig. 7).

(10) Cui et al. 2016 described ON-S Alpha as having a divisive suppression mechanism that explained the temporal properties of white-noise response better than a standard LN model. Do the authors think the divisive suppression reflects a property of the excitatory synapses independent of inhibition?

This is an interesting question, but one for which we don’t have a good answer for now. As mentioned in some of the above responses and as we have tried to clarify in the manuscript, we do not mean to imply that there is no role for presynaptic inhibition in modulating bipolar cell output, including for the divisive suppression described by Cui et al. Rather, our point is that the distinction between transient and sustained excitatory input to ON-T and ON-S RGCs does not require presynaptic inhibition and is more likely an intrinsic property of the bipolar cell synapses. 

(11) Do the authors mean to imply that the pool size at bipolar cell ribbon synapses could depend on the use of Ames vs. ACSF? 

For now, we do not have a good answer as to why there are quantitative differences in response kinetics between Ames and ACSF. We have not done any experiments to investigate whether ribbon sizes or ribbon pools are different in the different solutions.

(12) More generally, different mean luminance levels could drive different levels of baseline glutamate release, which could alter the available pool of vesicles at bipolar cell ribbon synapses. Can we explain varying degrees of transient/sustained in the same cell at different levels of mean luminance based on this mechanism (e.g., Grimes et al., 2014)?

Yes, the emergence of a transient component of excitatory input to ON-S RGCs at ~100 R*/rod/s versus at scotopic levels (0.5 R*/rod/s) in Grimes et al. (2014) could be due to differences in the number of releasable vesicles (due to different type 6 bipolar cell axon terminal membrane potentials and hence differences in spontaneous release rates) at the different light levels.

We should note that although ON-T and ON-S RGCs exhibit some changes in transient/sustained kinetics across different light levels, the relative differences between these RGC types are preserved across light levels. We have included a statement about this in the text (lines 361-367).

(13) Figure 1. Have the authors considered performing the LN analysis of the firing responses, to compare the degree of rectification between the two RGC types?

This is a good suggestions. From an LN analysis of spiking responses, we do not observe a clear difference between the static nonlinearity component of the model for ON-T and ON-S RGCs. Both RGC types are strongly rectified under our experimental conditions.  

(14) Figure 5. Do the authors have the pharmacology data for the ON-S cells? There are examples of sustained EPSCs in amacrine cells that become more transient after blocking inhibition, which at least suggests that inhibition can play some role in the transient/sustained nature of glutamate release (Park et al., 2015, Figure 3). Perhaps ON-S cells likewise become more transient with inhibition blocked. 

(The colored symbols in A were not visible in a printout. It would be useful to indicate the cell type (ON-T) in C and E). 

As described above in the response to reviewer 1’s recommendation for authors, we were not able to use SR95531/TPMPA for recordings from ON-S RGCs. Bath application of these drugs led to oscillatory bursts of excitatory input to ON-S RGCs. However, the lack of effect of bath-applied NBQX on the kinetics of glutamate release around either ON-T or ON-S RGC dendrites (new Fig. 7) suggests that presynaptic inhibition does not contribute to generating sustained excitation to ON-S RGCs (or transient excitation to ON-T RGCs).  

We have corrected Fig. 5A to include the referenced colored symbols and have also edited Fig 5C and E to clarify that measurements in Fig. 5C-F are from ON-T RGCs.

(15) Figure 6 legend. Should be Kcng4-Cre, not KCNG-Cre. Also, it should make clear that this is cre-dependent expression of iGluSnFR. For C, were the statistics based on the number of FOVs? 

Thanks for catching this, we have corrected Figure 6 legend. The methods section includes a description of how we achieved iGluSnFR expression on alpha RGC dendrites via a cre-dependent viral strategy in Kcng4-Cre mice.  We have also clarified that the statistics are based on ROIs in Figure 6C.

(16) Figure 7, Flashes were apparently 400% contrast on a dim background. What was the background? Is there a rod component to the response in this case? 

In Figure 7 (now Figure 8), the same background (~3300 R*/rod/s; 2000 P*/Scone/s) was used as in the Gaussian noise and step response experiments. At this light level, the response should be primarily be mediated by cones.

(17) Figure S1. The colors here differ from those in previous figures (Here, ON-T, magenta; ON-S, cyan). Is something mislabeled? 

Thanks for catching this. We mistakenly swapped the labels in the legend for Fig. S1. The figure colors were correct, but we have corrected the legend in the revised manuscript.

(18) Figure S2. For the LN model for RGC synaptic currents, the ON-S are more rectified than some previous recordings (Cui et al., 2016). Is this perhaps explained by different light levels?

We aren’t sure why ON-S excitatory currents are more strongly rectified in our recordings compared to Cui et al., 2016. Cui et al. used an ~20-fold higher background light intensity (~40,000 P*/cone/s vs. ~2000 P*/cone/s in our study), so different light levels may be a factor (although we should point out that rectification increases in these RGCs between scotopic to low photopic light levels (see Grimes et al., 2014 and Kuo et al., 2016).

(19) The study is apparently comparing PV1 and PV2 described in Farrow et al. (2013; see Supplementary information for stratification analysis), which should be cited.

Thanks, we have corrected this oversight in the revised manuscript. We now cite Farrow et al and mention the connection to PV1 and PV2 in the first paragraph of Results (lines 104-108).

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Reviewer #1

Major comments:

(comment #1)- It is interesting that TRF2 loss not only fails to increase γH2AX/53BP1 levels but may even slightly reduce them (e.g., Fig. S2c and the IF images). While the main hypothesis is that TRF2 loss does not trigger telomere dysfunction in NSCs, this observation raises the possibility that TRF2 itself contributes to DDR signaling (ATM-P, γH2AX, 53BP1) in these cells and that in its absence, cells are not able to form those foci. To exclude the possibility that telomere-specific DDR is being missed due to an overall dampened DDR response in the absence of TRF2, it would be informative to induce exogenous DSBs in TRF2-depleted cells and test DDR competence (e.g., IF for γH2AX/53BP1). In other words, are those NSC lacking TRF2 even able to form H2AX/53BP1 foci when damaged? In addition, it would be interesting to perform telomere fusion analysis in TRF2 silenced cells (and TRF1 silenced cells as a positive control).

We acknowledge a slight reduction; however, this difference is not statistically significant (Fig S2c,e). We will quantify the levels of DDR markers upon TRF2 loss and exogenous DSBs and include it in the subsequent revision.

(comment #2)-A TRF2 ChIP-seq should be performed in NSC as this list of genes (named TAN genes in the text) was determined using a ChIP performed in another cell line (HT1080). For the ChIP-qPCR in the various conditions, primers for negative control regions should be included to show the specific binding of TRF2 to the promoter of the genes associated with neuronal differentiation. For example, an intergenic region and/or promoters of genes that are not associated with neuronal differentiation (or don't contain a potential G4). The same comment goes true for the gene expression analysis: a few genes that are not bound by TRF2 should be included as negative controls to exclude a potential global effect of TRF2 loss on gene expression (ideally a RNA-seq would be performed instead). We have performed NSC-specific TRF2 ChIP-seq for an upcoming manuscript, which confirms TRF2 occupancy at multiple promoters of differentiation-associated genes. These data are provided solely for confidential evaluation by the designated reviewers.

Regarding the ChIP-qPCR control experiments: We thank reviewer for pointing this out, indeed we included controls in our PCR assays as positive (telomeric) and TRF2-nonbinding loci (GAPDH, RPS18, and ACTB, based on HT1080 TRF2 ChIP-seq data) as negative controls. These results were not included earlier for clarity given that we were presenting several ChIP-PCR figures - in response to the comment we have included this now in the revised version (Fig. S3d,e). Gene expression analyses show selective upregulation of the TAN genes upon TRF2 loss (data normalised to GAPDH); whereas negative control genes lacking TRF2 binding (RPS18, ACTB) remain unchanged, ruling out non-specific effects. (Fig S3f,g,j,k).

-(comment #3) A co-IP should be performed between the TRF2 PTM mutant K176R or WT TRF2 and REST and PRC2 components to directly show a defect of interaction between them when TRF2 is mutated (a co-IP with DNase/RNase treatment to exclude nucleic-acid bridging). The TRF2 PTM mutant T188N also seems to lead to an increased differentiation (Fig. S5a). Could the author repeat the measure of gene expression and co-IP with REST upon the overexpression of this mutant too?

We confirm that DNase/RNase is routinely included in our pull-down experiments to exclude nucleic-acid bridging, with detailed methodology now elaborated in the Methods section. Not including this in the manuscript Methods was an oversight from our side. Our data demonstrate that only REST directly interacts with TRF2, while TRF2 engages PRC2 indirectly via REST, as also previously shown by us and others (page 6; ref. [62]; Sharma et al., ref. [15]).

We thank the reviewer for noting the apparent differentiation in Fig. S5a. However, this observation represents rare spontaneous differentiation event and is not statistically significant (as shown in Fig S5b). Consistently, gene expression analysis of the TRF2-T188N mutant shows no significant change in TRF2-associated neuronal differentiation (TAN) genes. Therefore, Co-IP for TRF2-T188N with REST was not done.

(comment #4) - The authors show that the G4 ligands SMH14.6 and Bis-indole carboxamide upregulate TAN genes and promote neuronal differentiation, but the underlying mechanism remains unclear. Bis-indole carboxamide is generally considered a G4 stabilizer, while SMH14.6 is less characterized and should be better introduced. The authors should clarify how G4 stabilization would interfere with TRF2 binding, it seems that it would likely be by blocking access. A more detailed discussion, and ideally TRF2 ChIP after ligand treatment and/or G4 helicase treatment, would strengthen the model.

We clarify that Bis-indole carboxamide acts as a G4 stabilizer, while SMH14.6 is also a noted G4-binding ligand that stabilizes G4s (ref. [15]). The exclusion of TRF2 from G4 motifs in gene promoters by G4-binding ligands has also been documented previously (ref. [18]). In line with these findings, ChIP experiments performed following ligand treatment revealed a decreased occupancy of TRF2 at TAN gene promoters, supporting the proposed mechanism (added Fig. 6h).

Minor comments:

• Supp Figures related to the scRNA-seq are difficult to read (blurry).

Corrected

• Fig S1h: The red box mentioned in the legend is not visible

Corrected

• In the text, the Figures 1 f-g are misannotated as Fig 1m and l

Corrected

• The symbol γ of γH2AX is missing in the text

Corrected

• Fig.3d, please indicate in the legend that it is done in SH-SY5Y.

Added SH-SY5Y in the legend of Fig. 3d.

• Fig. S3b: Please consider replotting this panel with an increased y-axis scale. As currently presented, the TRF2 ChIP-seq peaks at several promoters appear truncated by the scaling.

Corrected

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

1. For most of the data graphs in the manuscript, there is no indication of the number of independent biological replicates carried out (which should ideally be plotted as individual dots overlaying the column graphs), or what the error bars represent, or what statistical test was used. All the figure legends and methods have now been updated with the corresponding biological replicates per experiment, with error bars as SD/SEM and the corresponding statistical test along with p values.

Figure S1.1a: needs a marker to show that the tissue is dentate gyrus.

We acknowledge the reviewers' concern that high-magnification images alone make it difficult to verify whether the fields are taken from the correct anatomical location. The dentate gyrus (DG) of the hippocampus is a well-defined structure. In the revised figure (Fig S1.1a), we now include a low-magnification image showing the entire hippocampus, including the CA fields, along with two high-magnification fields specifically from the DG region. Consistent with our claim, the co-immunostaining demonstrates that Sox2-positive neural stem cells in the DG are also positive for TRF2.

Figure 1c (and all other flow cytometry panels throughout the manuscript): it is not clear if the expression of any of these proteins, except maybe MAP2, are significantly different in the presence or absence of TRF2. These differences need to be presented more quantitatively, with the results compiled from multiple biological replicates and analysed statistically. I am not sure that flow cytometry is the best way to determine differences in protein expression levels for non-surface proteins, because many of the reported differences are not at all convincing.

To detect intracellular/nuclear proteins by flow cytometry, cells were permeabilized using pre-chilled 0.2% Triton X-100 for 10 minutes, as described in the Methods section.

We have revised the figures (Fig 1c,e) and now included statistical analysis from three independent biological replicates for these experiments.(Fig S1.4h-j, S2e, S6d)

Fig 1d: has TRF2 been effectively silenced in this experiment? There appears to be just as many TRF2+ nuclei in the "TRF2 silenced" panel vs the control, including in the cells with neurite outgrowths.

Quantification of nuclear levels of TRF2 showing decrease in nuclear TRF2 has been included in supplementary Fig S1g.

Fig 2a-c: these experiments need a positive control, showing increased expression of these proteins in mNSC and SH-SY5Y cells in response to a DNA damaging agent. Again, flow cytometry may not be the best method for this; immunofluorescence combined with telomere FISH would be more convincing.

We confirm that doxorubicin induces 53BP1 foci (IF-FISH Sup Fig. S2b) and TRF1 silencing elevates γH2AX (Sup Fig. S2c) validating DDR sensitivity. Unlike TRF2 loss (Fig. 2a-c), no TIFs appear with IF and telomere probes (Fig. 2d, Sup Fig. 2a), and without TIFs, there is no telomeric fusion. Flow cytometry was performed with Triton X- 100 to target nuclear protein. These findings adequately address the concern; therefore, further IF-FISH experiments were not included in the present study.

To conclude that telomere damage is not occurring, an independent marker of such damage, such as telomere fusions, should also be measured.

In response to uncapped telomeres, ATM kinase activates the DNA damage response (DDR), recruiting γH2AX and 53BP1 to telomeres, which precedes the end-to-end fusions (Takai et al., 2003; Maciejowski & de Lange, 2015; Takai et al., 2003; d'Adda di Fagagna et al., 2003; Cesare & Reddel, 2010; Hayashi et al., 2012; Sarek et al., 2015). We observe no DDR activation or foci (Fig. 2; Sup. Fig. 2). This absence of a DDR response and TIFs indicates no telomere uncapping, negating the need for direct telomere fusion analysis.

Figure S2b is lacking a no-doxorubicin control.

Untreated control has been included Fig. S2b.

Figures 3a and 3b need a positive control (e.g. TRF2 binding to telomeric DNA) and a negative control (e.g. a promoter that did not show any TRF2 binding in the HT1080 ChiP-seq experiment in Fig S3).

We have included positive (telomere) and negative (GAPDH) controls (based on HT1080 TRF2 ChIP-seq data) for the TRF2 ChIP assay in Supplementary Fig. S3d,e. Additionally, positive and negative controls for all ChIP experiments conducted in this study are presented in Supplementary Figs. S3d, S3e, S3h, S3i, S4c-h, and S5c-e

The data in Figure 3 would be more compelling if all experiments were also performed in fibroblasts to confirm the cell-type specificity of the effect.

Our HT1080 fibrosarcoma ChIP-seq data (ref. [18]; Sup. Fig. 3a,b) show TRF2 binding to TAN gene promoters in a fibroblast-derived model, with enrichment in neurogenesis-related genes (refs. [19,20]). In fibroblasts TRF2 depletion, as expected, induce telomere dysfunction and DDR (Fig. 2d; Sup. Fig. 2a), and eventually cell-cycle arrest and cell death as also reported earlier (van Steensel et al., 1998; Smogorzewska & de Lange, 2002). Therefore, the suggested experiments which would require sustained TRF2-depletion are not possible to perform in fibroblasts. TRF2 occupancy on the promoter of the genes in question in cells other than NSC was noted in HT1080 cells (ref. [18]; Sup. Fig. 3a,b).

No references are provided for the TRF2 posttranslational modifications on R17, K176, K190 and T188. What is the evidence for these modifications, and is it known if they participate in the telomeric role of TRF2?

These lines with references have been included in the manuscript (highlighted in blue).

R17 methylation enhances telomere stability (66). K176/K190 acetylation stabilizes telomeres and is deacetylated by SIRT6 (67). T188 phosphorylation facilitates telomere repair after DSBs(68). These PTMs primarily support telomeric roles.

The experiments in Fig 5 should also be performed with WT TRF2, to confirm that effects are not due to the overexpression of TRF2.

WT TRF2 shows no differentiation phenotype and change in TAN gene expression (Fig. 1f,g; 3h, Sup Fig. 5a). Confirming effects are not due to TRF2 overexpression.

Fig 5c has not been described in the text, and there are multiple technical problems with the TRF2 WT experiment: i) There appears to be significant background binding of REST to the IgG beads, though this blot has such high background it is hard to tell (the REST blot in Fig S4b is also of poor quality), ii) TRF2 is migrating at two different positions in the Input and IP lanes, and the TRF2 band in the K176R blot is at a different position to either, and iii) the relative loading of the Input and IP lanes is not indicated, so it's not clear why K176R appears to be so enriched in the IP.

We acknowledge the oversight in not citing Fig 5c in the manuscript. This has been corrected, and, highlighted in blue in the revised manuscript.

i) Multiple optimization attempts were made for the Co-IP experiments, and the presented figure reflects the best achievable result despite REST blot smearing, a pattern also reported previously (Ref. 65). The TRF2-REST interaction is well established, and a similar background was also observed in the cited study

ii)Variable migration patterns of TRF2 were also noted in the cited study (Ref. 65), consistent with our observations. Our primary emphasis, however, is on the TRF2 K176R mutant, which clearly disrupts its interaction with REST.

iii)The input loading corresponds to 10% of the total lysate. As the experiments were conducted independently, variations in transfection and pull-down efficiencies may account for observed differences.

To rule out indirect effects of the G4 ligands on the results in Fig 6g, the binding of BG4 and TRF2 at the promoters of these genes should be measured by ChIP.

To confirm that G4 ligand effects on TAN gene promoters are direct, TRF2 occupancy was assessed using ChIP. Significantly decreased occupancy of TRF2 was noted at TAN gene promoters, (added Fig. 6h). This implies that ligand-induced changes in TRF2 binding are directly linked to promoter-level G4 stabilization.

Minor comments:

1. The size of all the size markers in western blots should be added to the figures. Size has been included in all the western blots

2. There are several figure panels that are incorrectly referenced in the text, e.g. Fig S1.1 (e-f) should be Fig S1.1 (e-h); Fig. 1m should be Fig. 1f; Figs 5e and 5f have been swapped.

Corrected.

1. Fig S1.4 is not referred to in the text. It is not clear what the purpose of Fig S1.4a is.

The following line has been included in the manuscript highlighted in blue.

Neurospheres were characterized using PAX6, a NSC marker (Fig S1.4a).

Are the experiments in Figs 3e, 4a, 4c and 4e using 4-OHT treatment, or siRNA? If the latter, I don't think a control for the effectiveness of the knockdown in this cell type has been included anywhere in the manuscript.

It is using siRNA, a western blot showing the effectiveness of knockdown is presented in supplementary figure S4c (now S4a).

The lanes of the western blots in Fig S4c are not labelled.

Corrected.

1. Given that the experiments in Fig 5 were carried out on a background of endogenous WT TRF2 expression, presumably the K176R mutant is having a dominant negative effect. To understand the mechanism of this effect (e.g, is it simply due to replacement of endogenous WT TRF2 at its genomic binding sites by a large excess of exogenous K176R, or is dimerisation with WT TRF2 needed?) it would be helpful to know the relative expression levels of endogenous and K176R TRF2.

To address the query, qRT-PCR with 3′ UTR-specific primers showed no change in endogenous TRF2 mRNA upon K176R expression in SH-SY5Y cells, while primers detecting total TRF2 revealed ~10-fold higher expression of K176R compared to control (Figure below). This indicates the absence of suppression of endogenous TRF2 mRNA. Given that the mutant's DNA binding is intact (Fig. 5f), the dominant-negative effect of K176R likely arises from overexpression of the exogenous mutant.

For the sentence "...and critical for transcription factor binding including epigenetic functions that are G4 dependent" (bottom of page 3 of the PDF), the authors cite only their own prior papers, but there are examples from others that could be cited.

We have incorporated citations from other research groups, now included as references 23-26.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

We thank the reviewers for their thoughtful and constructive feedback, which helped us strengthen the study on both the computational and biological side. In response, we added substantial new analyses and results in a total of 26 new supplementary figures and a new supplementary note. Importantly, we demonstrated that our approach generalizes beyond tissue outcomes by predicting final-timepoint morphology clusters from early frames with good accuracy as new Figure 4C. Furthermore, we completely restructured and expanded the human expert panel: six experts now provided >30,000 annotations across evenly spaced time intervals, allowing us to benchmark human predictions against CNNs and classical models under comparable conditions. We verified that morphometric trajectories are robust: PCA-based reductions and nearest-neighbor checks confirmed that patterns seen in t-SNE/UMAP are genuine, not projection artifacts. To test whether z-stacks are required, we re-did all analyses with sum- and maximum-intensity projections across five slices; results were unchanged, showing that single-slice imaging is sufficient. From a bioinformatics perspective, we performed negative-label baselines, downsampling analyses to quantify dataset needs, and statistical tests confirming CNNs significantly outperform classical models. Biologically, we clarified that each well contains one organoid, further introduced the Latent Determination Horizon concept tied to expert visibility thresholds, and discussed limits in cross-experiment transfer alongside strategies for domain adaptation and adaptive interventions. Finally, we clarified methods, corrected terminology and a scaler leak, and made all code and raw data publicly available.

Together, these revisions in our opinion provide an even clearer, more reproducible, and stronger case for the utility of predictive modeling in retinal organoid development.

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

This study presents predictive modeling for developmental outcome in retinal organoids based on high-content imaging. Specifically, it compares the predictive performance of an ensemble of deep learning models with classical machine learning based on morphometric image features and predictions from human experts for four different task: prediction of RPE presence and lense presence (at the end of development) as well as the respective sizes. It finds that the DL model outperforms the other approaches and is predictive from early timepoints on, strongly indicating a time-frame for important decision steps in the developmental trajectory.

Response: We thank the reviewer for the constructive and thoughtful feedback. In response to the review as found below, we have made substantial revisions and additions to the manuscript. Specifically, we clarified key aspects of the experimental setup, changed terminology regarding training/validation/test sets, and restructured our human expert baseline analysis by collecting and integrating a substantially larger dataset of expert annotations according to suggestion. We introduced the Latent Determination Horizon concept with clearer rationale and grounding. Most importantly, we significantly expanded our interpretability analyses across three CNN architectures and eight attribution methods, providing comprehensive quantitative evaluations and supplementary figures that extend beyond the initial DenseNet121 examples (new Supplementary Figures S29-S37). We also ensured full reproducibility by making both code and raw data publicly available with documentation. While certain advanced interpretability methods (e.g., Discover) could not be integrated despite considerable effort, we believe the revised manuscript presents a robust, well-documented, and carefully qualified analysis of CNN predictions in retinal organoid development.

Major comments: I find the paper over-all well written and easy to understand. The findings are relevant (see significance statement for details) and well supported. However, I have some remarks on the description and details of the experimental set-up, the data availability and reproducibility / re-usability of the data.

1. Some details about the experimental set-up are unclear to me. In particular, it seems like there is a single organoid per well, as the manuscript does not mention any need for instance segmentation or tracking to distinguish organoids in the images and associate them over time. Is that correct? If yes, it should be explicitly stated so. Are there any specific steps in the organoid preparation necessary to avoid multiple organoids per well? Having multiple organoids per well would require the aforementioned image analysis steps (instance segmentation and tracking) and potentially add significant complexity to the analysis procedure, so this information is important to estimate the effort for setting up a similar approach in other organoid cultures (for example cancer organoids, where multiple organoids per well are common / may not be preventable in certain experimental settings).

Response: We thank the reviewer for this question. We agree that these preprocessing steps would add more complexity to our presented preprocessing steps and would definitely be required in some organoid systems. In our experimental setup, there is only one organoid per well which forms spontaneously after cell seeding from (almost) all seeded cells. There are no additional steps necessary in order to ensure this behaviour in our setup. We amended the Methods section to now explicitly state this accordingly (paragraph ‘Organoid timelapse imaging’).

The terminology used with respect to the test and validation set is contrary to the field, and reporting the results on the test set (should be called validation set), should be avoided since it is used to select models. In more detail: the terms "test set" and "validation set" (introduced in 213-221) are used with the opposite meaning to their typical use in the deep learning literature. Typically, the validation set refers to a separate split that is used to monitor convergence / avoid overfitting during training, and the test set refers to an external set that is used to evaluate the performance of trained models. The study uses these terms in an opposite manner, which becomes apparent from line 624: "best performing model ... judged by the loss of the test set.". Please exchange this terminology, it is confusing to a machine learning domain expert. Furthermore, the performance on the test set (should be called validation set) is typically not reported in graphs, as this data was used for model selection, and thus does not provide an unbiased estimate of model performance. I would remove the respective curves from Figures 3 and 4.

Response: We are thankful for the reviewers comments on this matter. Indeed, we were using an opposite terminology compared to what is commonly used within the field. We have adjusted the Results, Discussion and Methods sections as well as the figures accordingly. Further, we added a corresponding disclaimer for the code base in the github repository. However, we prefer to not remove the respective curves from the figures. We think that this information is crucial to interpret the variability in accuracy between organoids from the same experiments and organoids acquired from a different, independent experiment. The results suggest that the accuracy for organoids within the same experiments is still higher, indicating to users the potential accuracy drop resulting from independent experiments. As we think that this is crucial information for the interpretability of our results, we would like to still include it side-by-side with the test data in the figures.

The experimental set-up for the human expert baseline is quite different to the evaluation of the machine learning models. The former is based on the annotation of 4,000 images by seven expert, the latter based on a cross-validation experiments on a larger dataset. First of all, the details on the human expert labeling procedure is very sparse, I could only find a very short description in the paragraph 136-144, but did not find any further details in the methods section. Please add a methods section paragraph that explains in more detail how the images were chosen, how they were assigned to annotators, and if there was any redundancy in annotation, and if yes how this was resolved / evaluated. Second, the fact that the set-up for human experts and ML models is quite different means that these values are not quite comparable in a statistical sense. Ideally, human estimators would follow the same set-up as in ML (as in, evaluate the same test sets). However, this would likely prohibitive in the required effort, so I think it's enough to state this fact clearly, for example by adding a comment on this to the captions of Figure 3 and 4.

Response: We thank the reviewer for this constructive suggestion. We agree that the curves for human evaluations in the original draft were calculated differently compared to the curves for the classification algorithms, mostly stemming from feasibility of data set annotation at the time. In order to still address this suggestion, we went on to repeat and substantially expand the number of images annotated and thus revised the full human expert annotation. Each one of 6 human experts was asked to predict/interpret 6 images of each organoid within the full dataset. In order to select the images, we divided the time course (0-72h) into 6 evenly spaced intervals of 12 hours. For each interval, one image per organoid and human expert was randomly selected and assigned. This resulted in a total of 31,626 classified images (up from 4000 in the original version of the manuscript), from which the assigned images were overlapping between experts for each source interval but not for the individual images. We then changed the calculation of the curves to be the same as for the classification analysis: F1 data were calculated for each experiment over 6 timeframes and all experts, and plotted within the respective figure. We have amended the Methods section accordingly and replaced the respective curves within Figures 3 and 4 and Supplementary Figures S1, S8 and S19.

It is unclear to me where the theoretical time window for the Latent Determination Horizon in Figure 5 (also mentioned in line 350) comes from? Please explain this in more detail and provide a citation for it.

Response: We thank the reviewer for this important point. The Latent Determination Horizon (LDH) is a conceptual framework we introduced in this study to describe the theoretical period during which the eventual presence of a tissue outcome of interest (TOI) is being determined but not yet detectable. It is derived from two main observations in our dataset: (i) the inherent intra- and inter-experimental heterogeneity of organoid outcomes despite standardized protocols, and (ii) the progressive increase in predictive performance of our deep learning models over time, which suggests that informative morphological features only emerge gradually. We have now clarified this rationale in the manuscript (Discussion section) further and explicitly stated that the LDH is a concept we introduce here, rather than a previously described or cited term.

The timewindow is defined by the TOI visibility, which is defined empirically as indicated by the results of our human expert panel (compare also Supplementary Figure S1).

The intepretability analysis (Figure 4, 634-639) based on relevance backpropagation was performed based on DenseNet121 only. Why did you choose this model and not the ResNet / MobileNet? I think it is quite crucial to see if there are any differences between these model, as this would show how much weight can be put on the evidence from this analysis and I would suggest to add an additional experiment and supplementary figure on this.

Response: We thank the reviewer for this important comment regarding the interpretability analysis and the choice of model. In the original submission, we restricted the attribution analyses shown in originial Figure 4C to DenseNet121, which served as our main reference model throughout the study. This choice was made primarily for clarity and to avoid redundancy in the main figures, as all three convolutional neural network (CNN) architectures (DenseNet121, ResNet50, MobileNetV3_Large) achieved comparable classification performance on our tasks.

In response to the reviewer’s concern, we have now extended the interpretability analyses to include all three CNN architectures and a total of eight attribution methods (new Supplementary Note 1). Specifically, we generated saliency maps for DenseNet121, ResNet50, and MobileNetV3_Large across multiple time points and evaluated them using a systematic set of metrics: pairwise method agreement within each model (new Supplementary Figure S29), cross-model consistency per method (new Supplementary Figure S34), entropy and diffusion of saliencies over time (new Supplementary Figure S35), regional voting overlap across methods (new Supplementary Figure S36), and spatial drift of saliency centers of mass (new Supplementary Figure S37).

These pooled analyses consistently showed that attribution methods differ markedly in the regions they prioritize, but that their relative behaviors were mostly stable across the three CNN architectures. For example, Grad-CAM and Guided Grad-CAM exhibited strong internal agreement and progressively focused relevance into smaller regions, while gradient-based methods such as DeepLiftSHAP and Integrated Gradients maintained broader and more diffuse relevance patterns but were the most consistent across models. Perturbation-based methods like Feature Ablation and Kernel SHAP often showed decreasing entropy and higher spatial drift, again similarly across architectures.

To further address the reviewer’s point, we visualized the organoid depicted in original Figure 4C across all three CNNs and all eight attribution methods (new Supplementary Figures S30-S33). These comparisons confirm and extend analysis of the qualitative patterns described in original Figure 4C and show that they are not specific to DenseNet121, but are representative of the general behavior across architectures.

In sum, we observed notable differences in how relevance was assigned and how consistently these assignments aligned. Highlighted organoid patterns were not consistent enough across attribution methods for us to be comfortable to base unequivocal biological interpretation on them. Nevertheless we believe that the analyses in response to the reviewer’s suggestions (new Supplementary Note 1 and new Supplementary Figures S29-S37) add valuable context to what can be expected from machine learning models in an organoid research setting.

As we did not base further unequivocal biological claims on the relevance backpropagation, we decided to move the analyses to the Supporting Information and now show a new model predicting organoid morphology by morphometrics clustering at the final imaging timepoint in new Figure 4C in line with suggestions by Reviewer #3.

The code referenced in the code availability statement is not yet present. Please make it available and ensure a good documentation for reproducibility. Similarly, it is unclear to me what is meant by "The data that supports the findings will be made available on HeiDoc". Does this only refer to the intermediate results used for statistical analysis? I would also recommend to make the image data of this study available. This could for example be done through a dedicated data deposition service such as BioImageArchive or BioStudies, or with less effort via zenodo. This would ensure both reproducibility as well as potential re-use of the data. I think the latter point is quite interesting in this context; as the authors state themselves it is unclear if prediction of the TOIs isn't even possible at an earlier point that could be achieved through model advances, which could be studied by making this data available.

Response: We thank the reviewer for this comment. We have now made the repository and raw data public on the suggested platform (Zenodo) and apologize for this oversight. The links are contained within the github repository which is stated in the manuscript under “Data availability”.

Minor comments:

Line 315: Please add a citation for relevance backpropagation here.

Response: We have included citations for all relevance backpropagation methods used in the paper.

Line 591: There seems to be typo: "[...] classification of binary classification [...]"

Response: Corrected as suggested.

Line 608: "[...] where the images of individual organoids served as groups [...]" It is unclear to me what this means.

Response: We wanted to express that organoid images belonging to one organoid were assigned in full to a training/validation set. We have now stated this more clearly in the Methods section.

Reviewer #1 (Significance (Required)):

General assessment: This study demonstrates that (retinal) organoid development can be predicted from early timepoints with deep learning, where these cannot be discerned by human experts or simpler machine learning models. This fact is very interesting in itself due to its implication for organoid development, and could provide a valuable tool for molecular analysis of different organoid populations, as outlined by the authors. The contribution could be strengthened by providing a more thorough investigation of what features in the image are predictive at early timepoints, using a more sophisticated approach than relevance backprop, e.g. Discover (https://www.nature.com/articles/s41467-024-51136-9). This could provide further biological insight into the underlying developmental processes and enhance the understanding of retinal organoid development.

Response: We thank the reviewer for this assessment and suggestion. We agree that identifying image features predictive at early timepoints would add important biological context. We therefore attempted to apply Discover to our dataset. However, we were unable to get the system to run successfully. After considerable effort, we concluded that this approach could not be integrated into our current analysis. Instead, we report our substantially expanded results obtained with relevance backpropagation, which provided the most interpretable and reproducible insights for our study as described above (New Supplementary Note 1, new Supplementary Figures S29-S37).

Advance: similar studies that predict developmental outcome based on image data, for example cell proliferation or developmental outcome exist. However, to the best of my knowledge, this study is the first to apply such a methodology to organoids and convincingly shows is efficacy and argues is potential practical benefits. It thus constitutes a solid technical advance, that could be especially impactful if it could be translated to other organoid systems in the future.

Response: We thank the reviewer for this positive assessment of our work and for highlighting its novelty and potential impact. We are encouraged that the reviewer recognizes the value of applying predictive modeling to organoids and the opportunities this creates for translation to other organoid systems.

Audience: This research is of interest to a technical audience. It will be of immediate interest to researchers working on retinal organoids, who could adapt and use the proposed system to support experiments by better distinguishing organoids during development. To enable this application, code and data availability should be ensured (see above comments on reproducibility). It is also of interest to researchers in other organoid systems, who may be able to adapt the methodology to different developmental outcome predictions. Finally, it may also be of interest to image analysis / deep learning researchers as a dataset to improve architectures for predictive time series modeling.

My research background: I am an expert in computer vision and deep learning for biomedical imaging, especially in microscopy. I have some experience developing image analysis for (cancer) organoids. I don't have any experience on the wet lab side of this work.

Response: We thank the reviewer for this encouraging feedback and for recognizing the broad relevance of our work across retinal organoid research, other organoid systems, and the image analysis community. We are pleased that the potential utility of our dataset and methodology is appreciated by experts in computer vision and biomedical imaging. We have now made the repository and raw data public and apologize for this oversight. The links are provided in the manuscript under “Data availability”.

Constantin Pape

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary: Afting et al. present a computational pipeline for analyzing timelapse brightfield images of retinal organoids derived from Medaka fish. Their pipeline processes images along two paths: 1) morphometrics (based on computer vision features from skimage) and 2) deep learning. They discovered, through extensive manual annotation of ground truth, that their deep learning method could predict retinal pigmented epithelium and lens tissue emergence in time points earlier than either morphometrics or expert predictions. Our review is formatted based on the review commons recommendation.

Response: We thank the reviewer for the detailed and constructive feedback, which has greatly improved the clarity and rigor of our manuscript. In response, we have corrected a potential data leakage issue, re-ran the affected analyses, and confirmed that results remain unchanged. We clarified the use of data augmentation in CNN training, tempered some claims throughout the text, and provided stronger justification for our discretization approach together with new supplementary analyses (New Supplementary Figures S26, S27). We substantially expanded our interpretability analyses across three CNN architectures and eight attribution methods, quantified their consistency and differences (new Supplementary Figures S29, S34-S37, new Supplementary Note 1), and added comprehensive visualizations (New S30-S33). We also addressed technical artifact controls, provided downsampling analyses to support our statement on sample size sufficiency (new Supplementary Figure S28), and included negative-control baselines with shuffled labels in Figures 3 and 4. Furthermore, we improved the clarity of terminology, figures, and methodological descriptions, and we have now made both code and raw data publicly available with documentation. Together, we believe these changes further strengthen the robustness, reproducibility, and interpretability of our study while carefully qualifying the claims.

Major comments:

Are the key conclusions convincing?

Yes, the key conclusion that deep learning outperforms morphometric approaches is convincing. However, several methodological details require clarification. For instance, were the data splitting procedures conducted in the same manner for both approaches? Additionally, the authors note in the methods: "The validation data were scaled to the same range as the training data using the fitted scalers obtained from the training data." This represents a classic case of data leakage, which could artificially inflate performance metrics in traditional machine learning models. It is unclear whether the deep learning model was subject to the same issue. Furthermore, the convolutional neural network was trained with random augmentations, effectively increasing the diversity of the training data. Would the performance advantage still hold if the sample size had not been artificially expanded through augmentation?

Response: We thank the reviewer for raising these important methodological points. As Reviewer #1 correctly noted, our use of the terms validation and test may have contributed to confusion. To clarify: in the original analysis the scalers were fitted on the training and validation data and then applied to the test data. This indeed constitutes a form of data leakage. We have corrected the respective code, re-ran all analyses that were potentially affected, and did not observe any meaningful change in the reported results. The Methods section has been amended to clarify this important detail.

For the neural networks, each image was normalized independently (per image), without using dataset-level statistics, thereby avoiding any risk of data leakage.

Regarding data augmentation, the convolutional neural network was indeed trained with augmentations. Early experiments without augmentation led to severe overfitting, confirming that the performance advantage would not hold without artificially increasing the effective sample size. We have added a clarifying statement in the Methods section to make this explicit.

Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Their claims are currently preliminary, pending increased clarity and additional computational experiments described below.

Response: We believe our additionally performed computational experiments qualify all the claims we make in the revised version of the manuscript.

Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

• The authors discretize continuous variables into four bins for classification. However, a regression framework may be more appropriate for preserving the full resolution of the data. At a minimum, the authors should provide a stronger justification for this binning strategy and include an analysis of bin performance. For example, do samples near bin boundaries perform comparably to those near the bin centers? This would help determine whether the discretization introduces artifacts or obscures signals.

Response: We thank the reviewer for this thoughtful suggestion. We agree that regression frameworks can, in principle, preserve the full resolution of continuous outcome variables. However, in our setting we deliberately chose a discretization approach. First, the discretized outcome categories correspond to ranges of tissue sizes that are biologically meaningful and allow direct comparison to expert annotations. In practice, human experts also tend to judge tissue presence and size in categorical rather than strictly continuous terms, which was mirrored by our human expert annotation strategy. As we aimed to compare deep learning with classical machine learning models and with expert annotations across the same prediction tasks, a categorical outcome formulation provided the most consistent and fair framework. Secondly, the underlying outcome variables did not follow a normal distribution, but instead exhibited a skewed and heterogeneous spread. Regression models trained on such distributions often show biases toward the most frequent value ranges, which may obscure less common but biologically important outcomes. Discretization mitigated this issue by balancing the prediction task across defined size categories.

In line with the reviewer’s request, we have now analyzed the performance in relation to the distance of each sample from the bin center. These results are provided as new Supplementary Figures S26 and S27. Interestingly, for the classical machine learning classifiers, F1 scores tended to be somewhat higher for samples close to bin edges. For the convolutional neural networks, however, F1 scores were more evenly distributed across distances from bin centers. While the reason for this difference remains unclear, the analysis demonstrates that the discretization did not obscure predictive signals in either framework. We have amended the results section accordingly.

• The relevance backpropagation interpretation analysis is not convincing. The authors argue that the model's use of pixels across the entire image (rather than just the RPE region) indicates that the deep learning approach captures holistic information. However, only three example images are shown out of hundreds, with no explanation for their selection, limiting the generalizability of the interpretation. Additionally, it is unclear how this interpretability approach would work at all in earlier time points, particularly before the model begins making confident predictions around the 8-hour mark. It is also not specified whether the input used for GradSHAP matches the input used during CNN training. The authors should consider expanding this analysis by quantifying pixel importance inside versus outside annotated regions over time. Lastly, Figure 4C is missing a scale bar, which would aid in interpretability.

Response: We thank the reviewer for raising these important concerns. In the initial version we showed examples of relevance backpropagation that suggested CNNs rely on visible RPE or lens tissue for their predictions (original Figure 4C). Following the reviewer’s comment, we expanded the analysis extensively across all models and attribution methods (compare new Supplementary Note 1), and quantified agreement, consistency, entropy, regional overlap, and drift (new Supplementary Figures S29 and S34-S37), as well as providing comprehensive visualizations across models and methods (new Supplementary Figures S30-S33).

This extended analysis showed that attribution methods behave very differently from each other, but consistently so across the three CNN architectures. Each method displayed characteristic patterns, for example in entropy or center-of-mass drift, but the overlap between methods was generally low. While integrated gradients and DeepLiftSHAP tended to concentrate on tissue regions, other methods produced broader or shifting relevance patterns, and overall we could not establish robust or interpretable signals from a biological point of view that would support stronger conclusions.

We have therefore revised the text to focus on descriptive results only, without making claims about early structural information or tissue-specific cues being used by the networks. We also added missing scale bars and clarified methodological details. Together, the revised section now reflects the extensive work performed while remaining cautious about what can and cannot be inferred from saliency methods in this setting.

• The authors claim that they removed technical artifacts to the best of their ability, but it is unclear if the authors performed any adjustment beyond manual quality checks for contamination. Did the authors observe any illumination artifacts (either within a single image or over time)? Any other artifacts or procedures to adjust?

Response: We thank the reviewer for this comment. We have not performed any adjustment beyond manual quality control post organoid seeding. The aforementioned removal of technical artifacts included, among others, seeding at the same time of day, seeding and cell processing by the same investigator according to a standardized protocol, usage of reproducible chemicals (same LOT, frozen only once, etc.) and temperature control during image acquisition. We adhered strictly to internal, previously published workflows that were aimed to reduce any variability due to technical variations during cell harvesting, organoid preparation and imaging. We have clarified this important point in the Methods section.

• In line 434-436 the authors state "In this work, we used 1,000 organoids in total, to achieve the reported prediction accuracies. Yet, we suspect that as little as ~500 organoids are sufficient to reliably recapitulate our findings." It is unclear what evidence the authors use to support this claim? The authors could perform a downsampling analysis to determine tradeoff between performance and sample size.

Response: We thank the reviewer for this important comment. To clarify, our statement regarding the sufficiency of ~500 organoids was based on a downsampling-style analysis we had already performed. In this analysis, we systematically reduced the number of experiments used for training and assessed predictive performance for both CNN- and classifier-based approaches (former Supplementary Figure S11, new Supplementary Figure S28). For CNNs, performance curves plateaued at approximately six experiments (corresponding to ~500 organoids), suggesting that increasing the sample size further only marginally improved prediction accuracy. In contrast, we did not observe a clear plateau for the machine learning classifiers, indicating that these models can achieve comparable performance with fewer training experiments. We have revised the manuscript text to clarify that this conclusion is derived from these analyses, and continue to include Supplementary Figure S11 as new Supplementary Figure S28 for transparency (compare Supplementary Note 1).

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. Yes, we believe all experiments are realistic in terms of time and resources. We estimate all experiments could be completed in 3-6 months.

Response: We confirm that the suggested experiments are realistic in terms of time and resources and have been able to complete them within 6 months.

Are the data and the methods presented in such a way that they can be reproduced? No, the code is not currently available. We were not able to review the source code.

Response: We have now made the repository public. We apologize for this initial oversight. The links are provided in the revised version of the manuscript under “Data availability”.

Are the experiments adequately replicated and statistical analysis adequate?

• The experiments are adequately replicated.

• The statistical analysis (deep learning) is lacking a negative control baseline, which would be helpful to observe if performance is inflated.

Response: We thank the reviewer for this comment. We have calculated the respective curves with neural networks and machine learning classifiers that were trained on data with shuffled labels and have included these results as a separate curve in the respective Figures 3 and 4. We have also amended the Methods section accordingly.

Minor comments:

Specific experimental issues that are easily addressable.

Are prior studies referenced appropriately?

Yes.

Are the text and figures clear and accurate?

The authors must improve clarity on terminology. For example, they should define a comprehensive dataset, significant, and provide clarity on their morphometrics feature space. They should elaborate on what they mean by "confounding factor of heterogeneity".

Response: We thank the reviewer for highlighting the need to clarify terminology. We have revised the manuscript accordingly. Specifically, we now explicitly define comprehensive dataset as longitudinal brightfield imaging of ~1,000 organoids from 11 independent experiments, imaged every 30 minutes over several days, covering a wide range of developmental outcomes at high temporal resolution. Furthermore, we replaced the term significantly with wording that avoids implying statistical significance, where appropriate. We have clarified the morphometrics feature space in the Methods section in a more detailed fashion, describing the custom parameters that we used to enhance the regionprops_table function of skimage.

Do you have suggestions that would help the authors improve the presentation of their data and conclusions? - Figure 2C describes a distance between what? The y axis is likely too simple. Same confusion over Figure 2D. Was distance computed based on tsne coordinates?

Response: We thank the reviewer for pointing out this potential source of confusion. The distances shown in original Figures 2C and 2D were not calculated in tSNE space. Instead, morphometrics features were first Z-scaled, and then dimensionality reduction by PCA was applied, with the first 20 principal components retaining ~93% of the variance. Euclidean distances were subsequently computed in this 20-dimensional PC space. For inter-organoid distances (Figure 2C), we calculated mean pairwise Euclidean distances between all organoids at each imaging time point, capturing the global divergence of organoid morphologies over time in an experiment-specific manner. For intra-organoid distances (Figure 2D), we calculated Euclidean distances between consecutive time points (n vs. n+1) for each individual organoid, thereby quantifying the extent of morphological change within organoids over time. We have revised the Figure legend and Methods section to make these definitions clearer.

• The authors perform a Herculean analysis comparing dozens of different machine learning classifiers. They select two, but they should provide justification for this decision.

Response: We thank the reviewer for this comment. In our initial machine learning analyses, we systematically benchmarked a broad set of classifiers on the morphometrics feature space, using cross-validation and hyperparameter tuning where appropriate. The classifiers that we ultimately focused on were those that consistently achieved the best performance in these comparisons. This process is described in the Methods and summarized in the Supplementary Figures S4 and S15 (for sum- and maximum-intensity z-projections new Supplementary Figures S5/6 and S16/17), which show the results of the benchmarking. We have clarified the text to state that the selected classifiers were chosen on the basis of their superior performance in these evaluations.

• It would be good to get a sense for how these retinal organoids grow - are they moving all over the place? They are in Matrigel so maybe not, but are they rotating?

Can the author's approach predict an entire non-emergence experiment? The authors tried to standardize protocol, but ultimately if It's deriving this much heterogeneity, then how well it will actually generalize to a different lab is a limitation.

Response: We thank the reviewer for these thoughtful questions. The retinal organoids in our study were embedded in low concentrations of Matrigel and remained relatively stable in position throughout imaging. We did not observe substantial displacement or lateral movement of organoids, and no systematic rotation could be detected in our dataset. Small morphological rearrangements within organoids were observed, but the gross positioning of organoids within the wells remained consistent across time-lapse recordings.

Regarding generalization across laboratories, we agree with the reviewer that this is an important limitation. While we minimized technical variability by adhering to a highly standardized, published protocol (see Methods), considerable heterogeneity remained at both intra- and inter-experimental levels. This variability likely reflects inherent properties of the system, similar the reportings in the literature across organoid systems, rather than technical artifacts, and poses a potential challenge for applying our models to independently generated datasets. We therefore highlight the need for future work to test the robustness of our models across laboratories, which will be essential to determine the true generalizability of our approach. We have amended the Discussion accordingly.

• The authors should dampen claims throughout. For example, in the abstract they state, "by combining expert annotations with advanced image analysis". The image analysis pipelines use common approaches.

Response: We thank the reviewer for this comment. We agree that the individual image analysis steps we used, such as morphometric feature extraction, are based on well-established algorithms. By referring to “advanced image analysis,” we intended to highlight not the novelty of each single algorithm, but rather the way in which we systematically combined a large number of quantitative parameters and leveraged them through machine learning models to generate predictive insights into organoid development.

• The authors state: "the presence of RPE and lenses were disagreed upon by the two independently annotating experts in a considerable fraction of organoids (3.9 % for RPE, 2.9% for lenses).", but it is unclear why there were two independently annotating experts. The supplements say images were split between nine experts for annotation.

Response: We thank the reviewer for pointing out this ambiguity. To clarify, the ground truth definition at the final time point was established by two experts who annotated all organoids. These two annotators were part of the larger group of six experts who contributed to the earlier human expert annotation tasks. Thus, while six experts provided annotations for subsets of images during the expert prediction experiments, the final annotation for every single organoid at its last time frame was consistently performed by the same two experts to ensure a uniform ground truth. We have amended this in the revised manuscript to make this distinction clear.

• Details on the image analysis pipeline would be helpful to clarify. For example, why did they choose to measure these 165 morphology features? Which descriptors were used to quantify blur? Did the authors apply blur metrics per FOV or per segmented organoid?

Response: We thank the reviewer for this comment. To clarify, we extracted 165 morphometric features per segmented organoid, combining standard scikit-image region properties with custom implementations (e.g., blur quantified as the variance of the Laplace filter response within the organoid mask). All metrics, including blur, were calculated per segmented organoid rather than per full field of view. This broad feature space was deliberately chosen to capture size, shape, and intensity distributions in a comprehensive and unbiased manner. We now provide a more detailed description of the preprocessing steps, the full feature list, and the exact code implementations are provided in the Methods section (“Large-scale time-lapse Image analysis”) of the revised version of the manuscript as well as in the source code github repository.

• The description of the number of images is confusing and distracts from the number of organoids. The number of organoids and number of timepoints used would provide a better description of the data with more value. For example, does this image count include all five z slices?

Response: We thank the reviewer for this comment. The reported image count includes slice 3 only, which we based our models on. The five z-slices that we used to create the MAX- and SUM-intensity z-projections would increase this number 5-fold. While we agree that the number of organoids and time points are highly informative metrics and have provided these details in the manuscript, we also believe that reporting the image count is valuable, as it directly reflects the size of the dataset processed by our analysis pipelines. For this reason, we prefer to keep the current description.

• The authors should consider applying a maximum projection across the five z slices (rather than the middle z) as this is a common procedure in image analysis. Why not analyze three-dimensional morphometrics or deep learning features? Might this improve performance further?

Response: We thank the reviewer for this valuable suggestion. To address this point, we repeated all analyses using both sum- and maximum-intensity z-projections and have included the results as new Supplementary Figures S8-S10, S13/S14 for TOI emergence and new Supplementary Figures S19-S21, S24/S25 for TOI sizes (classifier benchmarking and hyperparameter tuning in new Supplementary Figures S5/S6 and S16/S17). These additional analyses did not reveal a noticeable improvement in performance, suggesting that projections incorporating all slices are not strictly necessary in our setting. An analysis that included all five z-slices separately for classification would indeed be of interest, but was not feasible within the scope of this study, as it would substantially increase the computational demands beyond the available resources and timeframe.

• There is a lot of manual annotation performed in this work, the authors could speculate how this could be streamlined for future studies. How does the approach presented enable streamlining?

Response: We thank the reviewer for raising this important point. The current study relied on expert visual review, which is time-intensive, but our findings suggest several ways to streamline future work. For instance, model-assisted prelabeling could be used to automatically accept high-confidence cases while routing only uncertain cases to experts. Active sampling strategies, focusing expert review on boundary cases or rare classes, as well as programmatic checks from morphometrics (e.g., blur or contrast to flag low-quality frames), could further reduce effort. Consensus annotation could be reserved only for cases where the model and expert disagree or confidence is low. Finally, new experiments could be bootstrapped with a small seed set of annotated organoids for fine-tuning before switching to such a model-assisted workflow. These possibilities are enabled by our approach, where organoids are imaged individually, morphometrics provide automated quality indicators, and the CNN achieves reliable performance at early developmental stages, making model-in-the-loop annotation a feasible and efficient strategy for future studies. We have added a clarifying paragraph to the Discussion accordingly.

Reviewer #2 (Significance (Required)):

Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The paper's advance is technical (providing new methods for organoid quality control) and conceptual (providing proof of concept that earlier time points contain information to predict specific future outcomes in retinal organoids)

Place the work in the context of the existing literature (provide references, where appropriate).

• The authors do a good job of placing their work in context in the introduction.

• The work presents a simple image analysis pipeline (using only the middle z slice) to process timelapse organoid images. So not a 4D pipeline (time and space), just 3D (time). It is likely that more and more of these approaches will be developed over time, and this article is one of the early attempts.

• The work uses standard convolutional neural networks.

Response: We thank the reviewer for this assessment. We agree that our work represents one of the early attempts in this direction, applying a straightforward pipeline with standard convolutional neural networks, and we appreciate the reviewer’s acknowledgment of how the study has been placed in context within the Introduction.

State what audience might be interested in and influenced by the reported findings. - Data scientists performing image-based profiling for time lapse imaging of organoids.

• Retinal organoid biologists

• Other organoid biologists who may have long growth times with indeterminate outcomes.

Response: We thank the reviewer for outlining the relevant audiences. We agree that the reported findings will be of interest to data scientists working on image-based profiling, retinal organoid biologists, and more broadly to organoid researchers facing long culture times with uncertain developmental outcomes.

Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. - Image-based profiling/morphometrics

• Organoid image analysis

• Computational biology

• Cell biology

• Data science/machine learning

• Software

This is a signed review:

Gregory P. Way, PhD

Erik Serrano

Jenna Tomkinson

Michael J. Lippincott

Cameron Mattson

Department of Biomedical Informatics, University of Colorado

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary:

This manuscript by Afting et. al. addresses the challenge of heterogeneity in retinal organoid development by using deep learning to predict eventual tissue outcomes from early-stage images. The central hypothesis is that deep learning can forecast which tissues an organoid will form (specifically retinal pigmented epithelium, RPE, and lens) well before those tissues become visibly apparent. To test this, the authors assembled a large-scale time-lapse imaging dataset of ~1,000 retinal organoids (~100,000 images) with expert annotations of tissue outcomes. They characterized the variability in organoid morphology and tissue formation over time, focusing on two tissues: RPE (which requires induction) and lens (which appears spontaneously). The core finding is that a deep learning model can accurately predict the emergence and size of RPE and lens in individual organoids at very early developmental stages. Notably, a convolutional neural network (CNN) ensemble achieved high predictive performance (F1-scores ~0.85-0.9) hours before the tissues were visible, significantly outperforming human experts and classical image-analysis-based classifiers. This approach effectively bypasses the issue of stochastic developmental heterogeneity and defines an early "determination window" for fate decisions. Overall, the study demonstrates a proof-of-concept that artificial intelligence can forecast organoid differentiation outcomes non-invasively, which could revolutionize how organoid experiments are analyzed and interpreted.

Recommendation:

While this manuscript addresses an important and timely scientific question using innovative deep learning methodologies, it currently cannot be recommended for acceptance in its present form. The authors must thoroughly address several critical limitations highlighted in this report. In particular, significant issues remain regarding the generalizability of the predictive models across different experimental conditions, the interpretability of deep learning predictions, and the use of Euclidean distance metrics in high-dimensional morphometric spaces-potentially leading to distorted interpretations of organoid heterogeneity. These revisions are essential for validating the general applicability of their approach and enhancing biological interpretability. After thoroughly addressing these concerns, the manuscript may become suitable for future consideration.

Response: We thank the reviewer for the thoughtful and constructive comments. In response, we expanded our analyses in several key ways. We clarified limitations regarding external datasets. Interpretability analyses were greatly extended across three CNN architectures and eight attribution methods (new Supplementary Figures S29-S37, new Supplementary Note 1), showing consistent but method-specific behaviors; as no reproducible biologically interpretable signals emerged, we now present these results descriptively and clearly state their limitations. We further demonstrated the flexibility of our framework by predicting morphometric clusters in addition to tissue outcomes (new Figure 4C), confirmed robustness of the morphometrics space using PCA and nearest-neighbor analyses (new Supplementary Figure S3), and added statistical tests confirming CNNs significantly outperform classical classifiers (Supplementary File 1). Finally, we made all code and raw data publicly available, clarified species context, and added forward-looking discussion on adaptive interventions. We believe these revisions now further improve the rigor and clarity of our work.

Major Issues (with Suggestions):

1. Generalization to Other Batches or Protocols: The drop in performance on independent validation experiments suggests the model may partially overfit to specific experimental conditions. A major concern is how well this approach would work on organoids from a different batch or produced by a slightly different differentiation protocol. Suggestion: The authors should clarify the extent of variability between their "independent experiment" and training data (e.g., were these done months apart, with different cell lines or minor protocol tweaks?). To strengthen confidence in the model's robustness, I recommend testing the trained model on one or more truly external datasets, if available (for instance, organoids generated in a separate lab or under a modified protocol). Even a modest analysis showing the model can be adapted (via transfer learning or re-training) to another dataset would be valuable. If new data cannot be added, the authors should explicitly discuss this limitation and perhaps propose strategies (like domain adaptation techniques or more robust training with diverse conditions) to handle batch effects in future applications.

Response: We thank the reviewer for this important comment. We fully agree with the reviewer that this would be an amazing addition to the manuscript. Unfortunately we are not able to obtain the requested external data set. Although retinal organoid systems exist and are widely used across different species lines, to the best of our knowledge our laboratory is the only one currently raising retinal organoids from primary embryonic pluripotent stem cells of Oryzias latipes and there is currently only one known (and published) differentiation protocol which allows the successful generation of these organoids. We note that our datasets were collected over the course of nine months, which already introduces variability across time and thus partially addresses concerns regarding batch effects. While we did not have access to truly external datasets (e.g., from other laboratories), we have clarified this limitation as suggested in the revised version of the manuscript and outlined strategies such as domain adaptation and training on more diverse conditions as promising future directions to improve robustness.

Biological Interpretation of Early Predictive Features: The study currently concludes that the CNN picks up on complex, non-intuitive features that neither human experts nor conventional analysis could identify. However, from a biological perspective, it would be highly insightful to know what these features are (e.g., subtle texture, cell distribution patterns, etc.). Suggestion: I encourage the authors to delve deeper into interpretability. They might try complementary explainability techniques (for example, occlusion tests where parts of the image are masked to see if predictions change, or activation visualization to see what patterns neurons detect) beyond GradientSHAP. Additionally, analyzing false predictions might provide clues: if the model is confident but wrong for certain organoids, what visual traits did those have? If possible, correlating the model's prediction confidence with measured morphometrics or known markers (if any early marker data exist) could hint at what the network sees. Even if definitive features remain unidentified, providing the reader with any hypothesis (for instance, "the network may be sensing a subtle rim of pigmentation or differences in tissue opacity") would add value. This would connect the AI predictions back to biology more strongly.

Response: We thank the reviewer for this thoughtful suggestion. We agree that linking CNN predictions to specific biological features would be highly valuable. In response, we expanded our interpretability analyses beyond GradientSHAP to a broad set of attribution methods and quantified their behavior across models and timepoints (new Supplementary Figures S29-S37, new Supplementary Note 1). While some methods (e.g., Integrated Gradients, DeepLiftSHAP) occasionally highlighted visible tissue regions, others produced diffuse or shifting relevance, and overall overlap was low. Therefore, our results did not yield reproducible, interpretable biological signals.

Given these results, we have refrained from speculating about specific early image features and now present the interpretability analyses descriptively. We agree that future studies integrating imaging with molecular markers will be required to directly link early predictive cues to defined biological processes.

Expansion to Other Outcomes or Multi-Outcome Prediction: The focus on RPE and lens is well-justified, but these are two outcomes within retinal organoids. A major question is whether the approach could be extended to predict other cell types or structures (e.g., presence of certain retinal neurons, or malformations) or even multiple outcomes at once. Suggestion: The authors should discuss the generality of their approach. Could the same pipeline be trained to predict, say, photoreceptor layer formation or other features if annotated? Are there limitations (like needing binary outcomes vs. multi-class)? Even if outside the scope of this study, a brief discussion would reassure readers that the method is not intrinsically limited to these two tissues. If data were available, it would be interesting to see a multi-label classification (predict both RPE and lens presence simultaneously) or an extension to other organoid systems in future. Including such commentary would highlight the broad applicability of this platform.

Response: We thank the reviewer for this helpful and important suggestion. While our study focused on RPE and lens as the most readily accessible tissues of interest in retinal organoids, our new analyses demonstrate that the pipeline is not limited to these outcomes. In addition to tissue-specific predictions, we trained both a convolutional neural network (on image data) and a decision tree classifier (on morphometrics features) to predict more abstract morphological clusters defined at the final timepoint using the morphometrics features, showing that both approaches could successfully capture non-tissue features from early frames (new Figure 4C). This illustrates that the framework can be extended beyond binary tissue outcomes to multi-class problems, and predict relevant outcomes like the overall organoid morphology. Given appropriate annotations, the framework could in principle be trained to detect additional structures such as photoreceptor layers or malformations. Furthermore, the CNN architecture we employed and the morphometrics feature space are compatible with multi-label classification, meaning simultaneous prediction of several outcomes would also be feasible. We have clarified this point in the discussion to highlight the methodological flexibility and potential generality of our approach and are excited to share this very interesting, additional model with the readership.

Curse of high dimensionality: Using Euclidean distance in a 165-dimensional morphometric space likely suffers from the curse of dimensionality, which diminishes the meaning of distances as dimensionality increases. In such high-dimensional settings, the range of pairwise distances tends to collapse, undermining the ability to discern meaningful intra- vs. inter-organoid differences. Suggestion: To address this, I would encourage the authors to apply principal component analysis (PCA) in place of (or prior to) tSNE. PCA would reduce the data to a few dominant axes of variation that capture most of the morphometric variance, directly revealing which features drive differences between organoids. These principal components are linear combinations of the original 165 parameters, so one can examine their loadings to identify which morphometric traits carry the most information - yielding interpretable axes of biological variation (e.g., organoid size, shape complexity, etc.). In addition, I would like to mention an important cautionary remark regarding tSNE embeddings. tSNE does not preserve global geometry of the data. Distances and cluster separations in a tSNE map are therefore not faithful to the original high-dimensional distances and should be interpreted with caution. See Chari T, Pachter L (2023), The specious art of single-cell genomics, PLoS Comput Biol 19(8): e1011288, for an enlightening discussion in the context of single cell genomics. The authors have shown that extreme dimensionality reduction to 2D can introduce significant distortions in the data's structure, meaning the apparent proximity or separation of points in a tSNE plot may be an artifact of the algorithm rather than a true reflection of morphometric similarity. Implementing PCA would mitigate high-dimensional distance issues by focusing on the most informative dimensions, while also providing clear, quantitative axes that summarize organoid heterogeneity. This change would strengthen the analysis by making the results more robust (avoiding distance artifacts) and biologically interpretable, as each principal component can be traced back to specific morphometric features of interest.

Response: We thank the reviewer for this mention. Indeed, high dimensionality and dimensionality reductions can lead to false interpretations. We approached this issue as follows: First, we calculated the same TSNE projections and distances using the first 20 PCs and supplied these data as the new Figure 2 and new Supplementary Figure 2. While the scale of the data shifted slightly, there were no differences in the data distribution that would contradict our prior conclusions.

In order to confirm the findings and further emphasize the validity of our dimensionality reduction, we calculated the intersection of 30 nearest neighbors in raw data space (or pca space) compared and 30 nearest neighbors in reduced space (TSNE or UMAP, as we wanted to emphasize that this was not an effect specific for TSNE projections and would also be valid in a dimensionality reduction which is more known to preserve global structure rather than local structure). As shown in the new Supplementary Figure S3 (A-D), the high jaccard index confirmed that our projections accurately reflect the data’s structure obtained from raw distance measurements. Moreover, the jaccard index generally increased over time, which is best explained by a stronger morphological similarity of organoids at timepoint 0 and reflected by the dense point cloud in the TSNE projections at that timepoint. The described effects were independent of the usage of data derived from 20 PCs versus data derived from all 165 dimensions.

We next wanted to confirm the conclusion that data points obtained from organoids at later timepoints were more closely related to each other than data points from different organoids. We therefore identified the 30 nearest neighbor data points, showing that at later timepoints these 30 nearest neighbor data points were almost all attributable to the same organoid (new Supplementary Figure S3 E/F). This was only not the case for experiments that lacked in between timepoints (E007 and E002), therefore misaligning the organoids in the reduced space and convoluting the nearest neighbor analysis.

We have included the respective new Figures and new Supplementary Figures and linked them in the main manuscript.

Statistical Reporting and Significance: The manuscript focuses on F1-score as the metric to report accuracy over time, which is appropriate. However, it's not explicitly stated whether any statistical significance tests were performed on the differences between methods (e.g., CNN vs human, CNN vs classical ML). Suggestion: The authors could report statistical significance of the performance differences, perhaps using a permutation test or McNemar's test on predictions. For example, is the improvement of the CNN ensemble over the Random Forest/QDA classifier statistically significant across experiments? Given the n of organoids, this should be assessable. Demonstrating significance would add rigor to the analysis.

Response: We thank the reviewer for this helpful suggestion. Following the recommendation, we quantified per-experiment differences in predictive performance by calculating the area under the F1-score curves (AUC) for each classifier and experiment. We then compared methods using paired Wilcoxon signed-rank tests across experiments, with Holm-Bonferroni correction for multiple comparisons. This analysis confirmed that the CNN consistently and significantly outperformed the baseline models and classical machine learning classifiers in validation and test organoids, while CNNs were notably but not significantly better performing in test organoids for RPE area and lens sizes compared to the machine learning classifiers. In summary, the findings add the requested statistical rigor to our findings. The results of these tests are now provided in the Supplementary Material as Supplementary File 1.

Minor Issues (with Suggestions):

1. Data Availability: Given the resource-intensive nature of the work, the value to the community will be highest if the data is made publicly available. I understand that this is of course at the behest of the authors and they do mention that they will make the data available upon publication of the manuscript. For the time being, the authors can consider sharing at least a representative subset of the data or the trained model weights. This will allow others to build on their work and test the method in other contexts, amplifying the impact of the study.

Response: We have now made the repository and raw data public and apologize for this oversight. The link for the github repository is now provided in the manuscript under “Data availability”, while the links for the datasets are contained within the github repository.

Discussion - Future Directions: The Discussion does a good job of highlighting applications (like guiding molecular analysis). One minor addition could be speculation on using this approach to actively intervene: for example, could one imagine altering culture conditions mid-course for organoids predicted not to form RPE, to see if their fate can be changed? The authors touch on reducing variability by focusing on the window of determination; extending that thought to an experimental test (though not done here) would inspire readers. This is entirely optional, but a sentence or two envisioning how predictive models enable dynamic experimental designs (not just passive prediction) would be a forward-looking note to end on.

Response: We thank the reviewer for this constructive suggestion. We have expanded the discussion to briefly address how predictive modeling could go beyond passive observation. Specifically, we now discuss that predictive models may enable dynamic interventions, such as altering culture conditions mid-course for organoids predicted not to form RPE, to test whether their developmental trajectory can be redirected. While outside the scope of the present work, this forward-looking perspective emphasizes how predictive modeling could inspire adaptive experimental strategies in future studies.

I believe with the above clarifications and enhancements - especially regarding generalizability and interpretability - the paper will be suitable for broad readership. The work represents an exciting intersection of developmental biology and AI, and I commend the authors for this contribution.

Response: We thank the reviewer for the positive assessment and their encouraging remarks regarding the contribution of our work to these fields.

Novelty and Impact:

This work fills an important gap in organoid biology and imaging. Previous studies have used deep learning to link imaging with molecular profiles or spatial patterns in organoids, but there remained a "notable gap" in predicting whether and to what extent specific tissues will form in organoids. The authors' approach is novel in applying deep learning to prospectively predict organoid tissue outcomes (RPE and lens) on a per-organoid basis, something not previously demonstrated in retinal organoids. Conceptually, this is a significant advance: it shows that fate decisions in a complex 3D culture model can be predicted well in advance, suggesting the existence of subtle early morphogenetic cues that only a sophisticated model can discern. The findings will be of broad interest to researchers in organoid technology, developmental biology, and biomedical AI.

Response: We thank the reviewer for this thoughtful and encouraging assessment. We agree that our study addresses an important gap by prospectively predicting tissue outcomes at the single-organoid level, and we appreciate the recognition that this represents a conceptual advance with relevance not only for retinal organoids but also for broader applications in organoid biology, developmental biology, and biomedical AI.

Methodological Rigor and Technical Quality:

The study is methodologically solid and carefully executed. The authors gathered a uniquely large dataset under consistent conditions, which lends statistical power to their analyses. They employ rigorous controls: an expert panel provided human predictions as a baseline, and a classical machine learning pipeline using quantitative image-derived features was implemented for comparison. The deep learning approach is well-chosen and technically sound. They use an ensemble of CNN architectures (DenseNet121, ResNet50, and MobileNetV3) pre-trained on large image databases, fine-tuning them on organoid images. The use of image segmentation (DeepLabV3) to isolate the organoid from background is appropriate to ensure the models focus on the relevant morphology. Model training procedures (data augmentation, cross-entropy loss with class balancing, learning rate scheduling, and cross-validation) are thorough and follow best practices. The evaluation metrics (primarily F1-score) are suitable for the imbalanced outcomes and emphasize prediction accuracy in a biologically relevant way. Importantly, the authors separate training, test, and validation sets in a meaningful manner: images of each organoid are grouped to avoid information leakage, and an independent experiment serves as a validation to test generalization. The observation that performance is slightly lower on independent validation experiments underscores both the realism of their evaluation and the inherent heterogeneity between experimental batches. In addition, the study integrates interpretability (using GradientSHAP-based relevance backpropagation) to probe what image features the network uses. Although the relevance maps did not reveal obvious human-interpretable features, the attempt reflects a commendable thoroughness in analysis. Overall, the experimental design, data analysis, and reporting are of high quality, supporting the credibility of the conclusions.

Response: We thank the reviewer for their very positive and detailed assessment. We appreciate the recognition of our efforts to ensure methodological rigor and reproducibility, and we agree that interpretability remains an important but challenging area for future work.

Reviewer #3 (Significance (Required)):

Scientific Significance and Conceptual Advances:

Biologically, the ability to predict organoid outcomes early is quite significant. It means researchers can potentially identify when and which organoids will form a given tissue, allowing them to harvest samples at the right moment for molecular assays or to exclude organoids that will not form the desired structure. The manuscript's results indicate that RPE and lens fate decisions in retinal organoids are made much earlier than visible differentiation, with predictive signals detectable as early as ~11 hours for RPE and ~4-5 hours for lens. This suggests a surprising synchronization or early commitment in organoid development that was not previously appreciated. The authors' introduction of deep learning-derived determination windows refines the concept of a developmental "point of no return" for cell fate in organoids. Focusing on these windows could help in pinpointing the molecular triggers of these fate decisions. Another conceptual advance is demonstrating that non-invasive imaging data can serve a predictive role akin to (or better than) destructive molecular assays. The study highlights that classical morphology metrics and even expert eyes capture mainly recognition of emerging tissues, whereas the CNN detects subtler, non-intuitive features predictive of future development. This underlines the power of deep learning to uncover complex phenotypic patterns that elude human analysis, a concept that could be extended to other organoid systems and developmental biology contexts. In sum, the work not only provides a tool for prediction but also contributes conceptual insights into the timing of cell fate determination in organoids.

Response: We thank the reviewer for this thoughtful and positive assessment. We agree that the determination windows provide a valuable framework to study early fate decisions in organoids, and we have emphasized this point in the discussion to highlight the biological significance of our findings.

Strengths:

The combination of high-resolution time-lapse imaging with advanced deep learning is innovative. The authors effectively leverage AI to solve a biological uncertainty problem, moving beyond qualitative observations to quantitative predictions. The study uses a remarkably large dataset (1,000 organoids, >100k images), which is a strength as it captures variability and provides robust training data. This scale lends confidence that the model isn't overfit to a small sample. By comparing deep learning with classical machine learning and human predictions, the authors provide context for the model's performance. The CNN ensemble consistently outperforms both the classical algorithms and human experts, highlighting the value added by the new method. The deep learning model achieves high accuracy (F1 > 0.85) at impressively early time points. The fact that it can predict lens formation just ~4.5 hours into development with confidence is striking. Performance remained strong and exceeded human capability at all assessed times. Key experimental and analytical steps (segmentation, cross-validation between experiments, model calibration, use of appropriate metrics) are executed carefully. The manuscript is transparent about training procedures and even provides source code references, enhancing reproducibility. The manuscript is generally well-written with a logical flow from the problem (organoid heterogeneity) to the solution (predictive modeling) and clear figures referenced.

Response: We thank the reviewer for this very positive and encouraging assessment of our study, particularly regarding the scale of our dataset, the methodological rigor, and the reproducibility of our approach.

Weaknesses and Limitations:

Generalizability Across Batches/Conditions: One limitation is the variability in model performance on organoids from independent experiments. The CNN did slightly worse on a validation set from a separate experiment, indicating that differences in the experimental batch (e.g., slight protocol or environmental variations) can affect accuracy. This raises the question of how well the model would generalize to organoids generated under different protocols or by other labs. While the authors do employ an experiment-wise cross-validation, true external validation (on a totally independent dataset or a different organoid system) would further strengthen the claim of general applicability.

Response: We thank the reviewer for this important point. We agree that generalizability across batches and experimental conditions is a key consideration. We have carefully revised the discussion to explicitly address this limitation and to highlight the variability observed between independent experiments.

Interpretability of the Predictions: Despite using relevance backpropagation, the authors were unable to pinpoint clear human-interpretable image features that drive the predictions. In other words, the deep learning model remains somewhat of a "black box" in terms of what subtle cues it uses at early time points. This limits the biological insight that can be directly extracted regarding early morphological indicators of RPE or lens fate. It would be ideal if the study could highlight specific morphological differences (even if minor) correlated with fate outcomes, but currently those remain elusive.

Response: We thank the reviewer for raising this important point. Indeed, while our models achieved robust predictive performance, the underlying morphological cues remained difficult to interpret using relevance backpropagation. We believe this limitation reflects both the subtlety of the early predictive signals and the complexity of the features captured by deep learning models, which may not correspond to human-intuitive descriptors. We have clarified this limitation in the Discussion and Supplementary Note 1 and emphasize that further methodological advances in interpretability, or integration with complementary molecular readouts, will be essential to uncover the precise morphological correlates of fate determination.

Scope of Outcomes: The study focuses on two particular tissues (RPE and lens) as the outcomes of interest. These were well-chosen as examples (one induced, one spontaneous), but they do not encompass the full range of retinal organoid fates (e.g., neural retina layers). It's not a flaw per se, but it means the platform as presented is specialized. The method might need adaptation to predict more complex or multiple tissue outcomes simultaneously.

Response: We agree with the reviewer that our study focuses on two specific tissues, RPE and lens, which served as proof-of-concept outcomes representing both induced and spontaneous differentiation events. While this scope is necessarily limited, we believe it demonstrates the general feasibility of our approach. We have clarified in the Discussion that the same framework could, in principle, be extended to additional retinal fates such as neural retina layers, or even to multi-label prediction tasks, provided appropriate annotations are available. We now provide additional experiments showing that even abstract morphological classes are well predictable. This will be an important next step to broaden the applicability of our platform.

Requirement of Large Data and Annotations: Practically, the approach required a very large imaging dataset and extensive manual annotation; each organoid's RPE and lens outcome, plus manual masking for training the segmentation model. This is a substantial effort that may be challenging to reproduce widely. The authors suggest that perhaps ~500 organoids might suffice to achieve similar results, but the data requirement is still high. Smaller labs or studies with fewer organoids might not immediately reap the full benefits of this approach without access to such imaging throughput.

Response: We thank the reviewer for highlighting this important point. We agree that the generation of a large imaging dataset and the associated annotations represent a substantial investment of time and resources. At the same time, we consider this effort highly relevant, as it reflects the intrinsic heterogeneity of organoid systems rather than technical artifacts, and therefore ensures robust model training. We have clarified this limitation in the discussion. While our full dataset included ~1,000 organoids, our downsampling analysis suggests that as few as ~500 organoids may already be sufficient to reproduce the key findings, which we believe makes the approach feasible for many organoid systems (compare new Supplementary Note 1). Moreover, as we outline in the Discussion, future refinements such as combining image- and tabular-based features or incorporating fluorescence data could further enhance predictive power and reduce annotation effort.

Medaka Fish vs. Other Systems: The retinal organoids in this study appear to be from medaka fish, whereas much organoid research uses human iPSC-derived organoids. It's not fully clear in the manuscript as to how the findings translate to mammalian or human organoids. If there are species-specific differences, the applicability to human retinal organoids (which are important for disease modeling) might need discussion. This is a minor point if the biology is conserved, but worth noting as a potential limitation.

Response: We thank the reviewer for pointing out this important consideration. We have now explicitly clarified in the Discussion that our proof-of-concept study was performed in medaka organoids, which offer high reproducibility and rapid development. While species-specific differences may exist, the predictive framework is not inherently restricted to medaka and should, in principle, be transferable to mammalian or human iPSC/ESC-derived organoids, provided sufficiently annotated datasets are available. We have amended the Discussion accordingly.

Predicting Tissue Size is Harder: The model's accuracy in predicting how much tissue (relative area) an organoid will form, while good, is notably lower than for simply predicting presence/absence. Final F1 scores for size classes (~0.7) indicate moderate success. This implies that quantitatively predicting organoid phenotypic severity or extent is more challenging, perhaps due to more continuous variation in size. The authors do acknowledge the lower accuracy for size and treat it carefully.

Response: We thank the reviewer for this observation and agree with their interpretation. We have already acknowledged in the manuscript that predicting tissue size is more challenging than predicting tissue presence/absence, and we believe we have treated these results with appropriate caution in the revised version of the manuscript.

Latency vs. Determination: While the authors narrow down the time window of fate determination, it remains somewhat unclear whether the times at which the model reaches high confidence truly correspond to the biological "decision point" or are just the earliest detection of its consequences. The manuscript discusses this caveat, but it's an inherent limitation that the predictive time point might lag the actual internal commitment event. Further work might be needed to link these predictions to molecular events of commitment.

Response: We agree with the reviewer. As noted in the Discussion, the time points identified by our models likely reflect the earliest detectable morphological consequences of fate determination, rather than the exact molecular commitment events themselves. Establishing a direct link between predictive signals and underlying molecular mechanisms will require future experimental work.

Last year, Addie annotated this exact section and described how Eliot purposefully confuses the reader's sense of right-side-up and upside-down. In an especially insightful section of analysis she claims that if the reader were to orient herself with respect to Dracula (whom "crawled head downward down a blackened wall"), the tower down which he crawls becomes inverted - and the corresponding Tarot Card, the Dark Tower, is similarly flipped. Nested in this idea is a broader understanding: that in the chaos and turbulency of the modern world, the only form of agency we truly have is our perspective. When Dracula is flipped upside down, the world appears to him inverted; and though in fact it remains exactly the same as it always was, in his mind's eye all has been reoriented. That's precisely Eliot's point. Though the world itself may be a wasteland, there exists a copy of this world - a world of shadows, of impressions, of perspectives and opinions - which is completely up to interpretation. I think he invokes Tarot as a way of imbuing this doppelganger realm with purpose and value: Tarot is all about perspective. Your interpretation of the card, and what it tells you about your life in this theoretical duplicate of reality, informs the way you act in the real physical world - and so perhaps our agency, though constrained to our own perspectives, is more powerful than we think. The following two lines are relevant insofar as they condense several central thematic discussions: the voices, time, familiarity and remembrance, and water. All of these strands weave together a picture of reality IN FACT: that is, a world in which people are consigned to make the same mistakes over and over, a world where several voices overlap but never really hear one another, a world analogous to a dry rock. I think Eliot piles up all these images to drive home the fact that though our perspectives may change (though the Dark Tower may become inverted, or vice versa), objective reality is constant. In this way he DOES put a pessimistic constraint on the extent to which our conception of life can actually influence the events occuring around us; but nevertheless I do think there are some shards of positivity embedded in there.

This line stood out to me due to its connection with the title "What the Thunder said," and similar connotation to the Gospel of John. This line appears after a somewhat odd repetition of a lack of water within the land. Rather, the speaker is left in a desolate landscape of "only rock." One may think that this baren image would also prompt a stillness of silence in nature. However, Eliot is quick to point out the presence of loud booms of thunder in my highlighted line. In particular, the thunder is "dry and sterile," therefor connecting to the state of the land; the rocky terrain is indeed also dry due to the emphasized absence of water and also sterile as a result. In The Gospel of John (line 29), thunder holds a contrasting purpose. 29] The people therefore, that stood by, and heard it, said that it thundered: others said, An angel spake to him. Therefore, the voice of God in John is expressed through thunder, showing the great force of divinity over the world. However, Eliot's vivid descriptions of the thunder in his wasteland could not be more different. The thunder is "dry and sterile." and in my opinion, lacks the religious importance evident in John, In connection the title, my reading of this line suggests that Eliot does not believe the thunder is saying anything (What the Thunder Said). Instead, we are trapped in a dry and sterile land mass with no divine connection to guide us out.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Manuscript number: RC-2024-02830

Corresponding author(s): Julien, Sage

1. General Statements

We thank the Reviewers for a fair review of our work and helpful suggestions. We have significantly revised the manuscript in response to these suggestions. We provide a point-by-point response to the Reviewers below but wanted to highlight in our response a recurring concern related to the strong cell cycle arrest observed upon the acute FAM53C knock-down being different than the limited phenotypes in other contexts, including the knockout mice and DepMap data.

First, we now show that we can recapitulate the strong G1 arrest resulting from the FAM53C knock-down using two independent siRNAs in RPE-1 cells, supporting the specificity of the effects.

Second, the G1 arrest that results from the FAM53C knock-down is also observed in cells with inactive p53, suggesting it is not due to a non-specific stress response due to “toxic” siRNAs. In addition, the arrest is dependent on RB, which fits with the genetic and biochemical data placing FAM53C upstream of RB, further supporting a specific phenotype.

Third, we have performed experiments in other human cells, including cancer cell lines. As would be expected for cancer cells, the G1 arrest is less pronounced but is still significant, indicating that the G1 arrest is not unique to RPE-1 cells.

Fourth, it is not unexpected that compensatory mechanisms would be activated upon loss of FAM53C during development or in cancer – which may explain the lack of phenotypes in vivo or upon long-term knockout. This has been true for many cell cycle regulators, either because of compensation by other family members that have overlapping functions, or by a larger scale rewiring of signaling pathways.

2. Point-by-point description of the revisions

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

Summary:

Taylar Hammond and colleagues identified new regulators of the G1/S transition of the cell cycle. They did so by screening public available data from the Cancer Dependency Map, and identified FAM53C as a positive regulator of the G1/S transition. Using biochemical assays they then show that FAM53 interacts with the DYRK1A kinase to inhibit its function. DYRK1A in its is known to induce degradation of cyclin D, leading the authors to propose a model in which DYRK1A-dependent cyclin D degradation is inhibited by FAM53C to permit S-phase entry. Finally the authors assess the effect of FAM53C deletion in a cortical organoid model, and in Fam53c knockout mice. Whereas proliferation of the organoids is indeed inhibited, mice show virtually no phenotype.

Major comments:

The authors show convincing evidence that FAM53C loss can reduce S-phase entry in cell cultures, and that it can bind to DYRK1A. However, FAM53 has multiple other binding partners and I am not entirely convinced that negative regulation of DYRK1A is the predominant mechanism to explain its effects on S-phase entry. Some of the claims that are made based on the biochemical assays, and on the physiological effects of FAM53C are overstated. In addition, some choices made methodology and data representation need further attention.

1. The authors do note that P21 levels increase upon FAM53C. They show convincing evidence that this is not a P53-dependent response. But the claim that " p21 upregulation alone cannot explain the G1 arrest in FAM53C-deficient cells (line 138-139) is misleading. A p53-independent p21 response could still be highly relevant. The authors could test if FAM53C knockdown inhibits proliferation after p21 knockdown or p21 deletion in RPE1 cells. The Reviewer raises a great point. Our initial statement needed to be clarified and also need more experimental support. We have performed experiments where we knocked down FAM53C and p21 individually, as well as in combination, in RPE-1 cells. These experiment show that p21 knock-down is not sufficient to negate the cell cycle arrest resulting from the FAM53C knock-down in RPE-1 cells (Figure 4B,C and Figure S4C,D).

We now extended these experiments to conditions where we inhibited DYRK1A, and we also compared these data to experiments in p53-null RPE-1 cells. Altogether, these experiments point to activation of p53 downstream of DYRK1A activation upon FAM53C knock-down, and indicate that p21 is not the only critical p53 target in the cell cycle arrest observed in FAM53C knock-down cells (Figure 4 and Figure S4).

The authors do not convincingly show that FAM53C acts as a DYRK1A inhibitor in cells. Figures 4B+C and S4B+C show extremely faint P-CycD1 bands, and tiny differences in ratios. The P values are hovering around the 0.05, so n=3 is clearly underpowered here. Total CycD1 levels also correlate with FAM53C levels, which seems to affect the ratios more than the tiny pCycD1 bands. Why is there still a pCycD1 band visible in 4B in the GFP + BTZ + DYRK1Ai condition? And if I look at the data points I honestly don't understand how the authors can conclude from S4C that knockdown of siFAM53C increases (DYRK1A dependent) increases in pCycD1 (relative to total CycD1). In figure 5C, no blot scans are even shown, and again the differences look tiny. So the authors should either find a way to make these assays more robust, or alter their claims appropriately.

We appreciate these comments from the Reviewer and have significantly revised the manuscript to address them.

The analysis of Cyclin D phosphorylation and stability are complicated by the upregulation of p21 upon FAM53C knock-down, in particular because p21 can be part of Cyclin D complexes, which may affect its protein levels in cells (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). Instead of focusing on Cyclin D levels and stability, we refocused the manuscript on RB and p53 downstream of FAM53C loss.

We removed previous panel 4B from the revised manuscript. For panels 4E and S4B (now panels S3J and S3K)), we used a true “immunoassay” (as indicated in the legend – not an immunoblot), which is much more quantitative and avoids error-prone steps in standard immunoblots (“Western blots”). Briefly, this system was developed by ProteinSimple. It uses capillary transfer of proteins and ELISA-like quantification with up to 6 logs of dynamic range (see their web site https://www.proteinsimple.com/wes.html). The “bands” we show are just a representation of the luminescence signals in capillaries. We made sure to further clarify the figure legends in the revised manuscript.

The representative Western blot images for 5C-D (now 5F-G) in the original submission are shown in Figure 5E, we apologize if this was not clear. The differences are small, which we acknowledge in the revised manuscript. Note that several factors can affect Cyclin D levels in cells, including the growth rate and the stage of the cell cycle. Our FACS analysis shows that normal organoids have ~63% of cells in G1 and ~13% in S phase; the overall lower proportion of S-phase cells in organoids may make the immunoblot difference appear smaller, with fewer cycling cells resulting in decreased Cyclin D phosphorylation.

Nevertheless, the Reviewer brings up a good point and comments from this Reviewer and the others made us re-think how to best interpret our results. As discussed above, we re-read carefully the Meyer paper and think that FAM53C’s role and DYRK1A activity in cells may be understood when considering levels of both CycD and p21 at the same time in a continuum. While our genetic and biochemical data support a role for FAM53C in DYRK1A inhibition, it is likely that the regulation of cell cycle progression by FAM53C is not exclusively due to this inhibition. As discussed above and below, we noted an upregulation of p21 upon FAM53C knock-down, and activation of p53 and its targets likely contributes significantly to the phenotypes observed. We added new experiments to support this more complex model (Figure 4 and Figure S4, with new model in S4L).

The experiments to test if DYRK1A inhibition could rescue the G1 arrest observed upon FAM53C knockdown are not entirely convincing either. It would be much more convincing if they also perform cell counting experiments as they have done in Figures 1F and 1G, to complement the flow cytometry assays. I suggest that the authors do these cell counting experiments in RPE1 +/- P53 cells as well as HCT116 cells. In addition, did the authors test if P21 is induced by DYRK1Ai in HCT116 cells?

We repeated the experiments with the DYRK1A inhibitor and counted the cells. In p53-null RPE-1 cells, we found that cell numbers do not increase in these conditions where we had observed a cell cycle re-entry (Fig. 4E), which was accompanied by apoptotic cell death (Fig. S4I). Thus, cells re-enter the cell cycle but die as they progress through S-phase and G2/M. We note that inhibition of DYRK1A has been shown to decrease expression of G2/M regulators (PMID: 38839871), which may contribute to the inability of cells treated to DYRK1Ai to divide. Because our data in RPE-1 cells showed that p21 knock-down was not sufficient to allow the FAM53C knock-down cells to re-enter the cell cycle, we did not further analyze p21 in HCT-116 cells.

The data in Figure 5C and 5D are identical, although they are supposed to represent either pCycD1 ratios or p21 levels. This is a problem because at least one of the two cannot be true. Please provide the proper data and show (representative) images of both data types.

We apologize for these duplicated panels in the original submission. We now replaced the wrong panel with the correct data (Fig. 5F,G).

Line 246: "Fam53c knockout mice display developmental and behavioral defects." I don't agree with this claim. The mutant mice are born at almost the expected Mendelian ratios, the body weight development is not consistently altered. But more importantly, no differences in adult survival or microscopic pathology were seen. The authors put strong emphasis on the IMPC behavioral analysis, but they should be more cautious. The IMPC mouse cohorts are tested for many other phenotypes related to behavior and neurological symptoms and apparently none of these other traits were changed in the IMPC Famc53c-/- cohort. Thus, the decreased exploration in a new environment could very well be a chance finding. The authors need to take away claims about developmental and behavioral defects from the abstract, results and discussion sections; the data are just too weak to justify this.

We agree with the Reviewer that, although we observed significant p-values, this original statement may not be appropriate in the biological sense. We made sure in the revised manuscript to carefully present these data.

Minor comments:

Can the authors provide a rationale for each of the proteins they chose to generate the list of the 38 proteins in the DepMap analysis? I looked at the list and it seems to me that they do not all have described functions in the G1/S transition. The analysis may thus be biased.

To address this point, we updated Table S1 (2nd tab) to provide a better rationale for the 38 factors chosen. Our focus was on the canonical RB pathway and we included RB binding proteins whose function had suggested they may also be playing a role in the G1/S transition. We do agree that there is some bias in this selection (e.g., there are more RB binding factors described) but we hope the Reviewer will agree with us that this list and the subsequent analysis identified expected factors, including FAM53C. Future studies using this approach and others will certainly identify new regulators of cell cycle progression.

Figure 1B is confusing to me. Are these just some (arbitrarily) chosen examples? Consider leaving this heatmap out altogether, of explain in more detail.

We agree with the Reviewer that this panel was not necessarily useful and possibly in the wrong place, and we removed it from the manuscript. We replaced it with a cartoon of top hits in the screen.

The y-axes in Figures 2C, 2D, 2E, and 4D are misleading because they do not start at 0. Please let the axis start at 0, or make axis breaks.

We re-graphed these panels.

Line 229: " Consequences ... brain development." This subheader is misleading, because the in vitro cortical organoid system is a rather simplistic model for brain development, and far away from physiological brain development. Please alter the header.

We changed the header to “Consequences of FAM53C inactivation in human cortical organoids in culture”.

Figure S5F: the gating strategy is not clear to me. In particular, how do the authors know the difference between subG1 and G1 DAPI signals? Do they interpret the subG1 as apoptotic cells? If yes, why are there so many? Are the culturing or harvesting conditions of these organoids suboptimal? Perhaps the authors could consider doing IF stainings on EdU or BrdU on paraffin sections of organoids to obtain cleaner data?

Thank you for your feedback. The subG1 population in the original Figure S5F represents cells that died during the dissociation step of the organoids for FACS analysis. To address this point, we performed live & dead staining to exclude dead cells and provide clearer data. We refined gating strategy for better clarity in the new S5F panel.

Figure S6A; the labeling seems incorrect. I would think that red is heterozygous here, and grey mutant.

We fixed this mistake, thank you.

__Reviewer #1 (Significance (Required)): __

The finding that the poorly studied gene FAM53C controls the G1/S transition in cell lines is novel and interesting for the cell cycle field. However, the lack of phenotypes in Famc53-/- mice makes this finding less interesting for a broader audience. Furthermore, the mechanisms are incompletely dissected. The importance of a p53-indepent induction of p21 is not ruled out. And while the direct inhibitory interaction between FAM53C and DYRK1A is convincing (and also reported by others; PMID: 37802655), the authors do not (yet) convincingly show that DYRK1A inhibition can rescue a cell proliferation defect in FAM53C-deficient cells.

Altogether, this study can be of interest to basic researchers in the cell cycle field.

I am a cell biologist studying cell cycle fate decisions, and adaptation of cancer cells & stem cells to (drug-induced) stress. My technical expertise aligns well with the work presented throughout this paper, although I am not familiar with biolayer interferometry.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

Summary

In this study Hammond et al. investigated the role of Dual-specificity Tyrosine Phosphorylation regulated Kinase 1A (DYRK1) in G1/S transition. By exploiting Dependency Map portal, they identified a previously unexplored protein FAM53C as potential regulator of G1/S transition. Using RNAi, they confirmed that depletion of FAM53C suppressed proliferation of human RPE1 cells and that this phenotype was dependent on the presence protein RB. In addition, they noted increased level of CDKN1A transcript and p21 protein that could explain G1 arrest of FAM53C-depleted cells but surprisingly, they did not observe activation of other p53 target genes. Proteomic analysis identified DYRK1 as one of the main interactors of FAM53C and the interaction was confirmed in vitro. Further, they showed that purified FAM53C blocked the ability of DYRK1 to phosphorylate cyclin D in vitro although the activity of DYRK1 was likely not inhibited (judging from the modification of FAM53C itself). Instead, it seems more likely that FAM53C competes with cyclin D in this assay. Authors claim that the G1 arrest caused by depletion of FAM53C was rescued by inhibition of DYRK1 but this was true only in cells lacking functional p53. This is quite confusing as DYRK1 inhibition reduced the fraction of G1 cells in p53 wild type cells as well as in p53 knock-outs, suggesting that FAM53C may not be required for regulation of DYRK1 function. Instead of focusing on the impact of FAM53C on cell cycle progression, authors moved towards investigating its potential (and perhaps more complex) roles in differentiation of IPSCs into cortical organoids and in mice. They observed a lower level of proliferating cells in the organoids but if that reflects an increased activity of DYRK1 or if it is just an off target effect of the genetic manipulation remains unclear. Even less clear is the phenotype in FAM53C knock-out mice. Authors did not observe any significant changes in survival nor in organ development but they noted some behavioral differences. Weather and how these are connected to the rate of cellular proliferation was not explored. In the summary, the study identified previously unknown role of FAM53C in proliferation but failed to explain the mechanism and its physiological relevance at the level of tissues and organism. Although some of the data might be of interest, in current form the data is too preliminary to justify publication.

Major points

1. Whole study is based on one siRNA to Fam53C and its specificity was not validated. Level of the knock down was shown only in the first figure and not in the other experiments. The observed phenotypes in the cell cycle progression may be affected by variable knock-down efficiency and/or potential off target effects. We thank the Reviewer for raising this important point. First, we need to clarify that our experiments were performed with a pool of siRNAs (not one siRNA). Second, commercial antibodies against FAM53C are not of the best quality and it has been challenging to detect FAM53C using these antibodies in our hands – the results are often variable. In addition, to better address the Reviewer’s point and control for the phenotypes we have observed, we performed two additional series of experiments: first, we have confirmed G1 arrest in RPE-1 cells with individual siRNAs, providing more confidence for the specificity of this arrest (Fig. S1B); second, we have new data indicating that other cell lines arrest in G1 upon FAM53C knock-down (Fig. S1E,F and Fig. 4F).

Experiments focusing on the cell cycle progression were done in a single cell line RPE1 that showed a strong sensitivity to FAM53C depletion. In contrast, phenotypes in IPSCs and in mice were only mild suggesting that there might be large differences across various cell types in the expression and function of FAM53C. Therefore, it is important to reproduce the observations in other cell types.

As mentioned above, we have new data indicating that other cell lines arrest in G1 upon FAM53C knock-down (three cancer cell lines) (Fig. S1E,F and Fig. 4F).

Authors state that FAM53C is a direct inhibitor of DYRK1A kinase activity (Line 203), however this model is not supported by the data in Fig 4A. FAM53C seems to be a good substrate of DYRK1 even at high concentrations when phosphorylations of cyclin D is reduced. It rather suggests that DYRK1 is not inhibited by FAM53C but perhaps FAM53C competes with cyclin D. Further, authors should address if the phosphorylation of cyclin D is responsible for the observed cell cycle phenotype. Is this Cyclin D-Thr286 phosphorylation, or are there other sites involved?

We revised the text of the manuscript to include the possibility that FAM53C could act as a competitive substrate and/or an inhibitor.

We removed most of the Cyclin D phosphorylation/stability data from the revised manuscript. As the Reviewers pointed out, some of these data were statistically significant but the biological effects were small. As discussed above in our response to Reviewer #1, the analysis of Cyclin D phosphorylation and stability are complicated by the upregulation of p21 upon FAM53C knock-down, in particular because p21 can be part of Cyclin D complexes, which may affect its protein levels in cells (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). Instead of focusing on Cyclin D levels and stability, we refocused the manuscript on RB and p53 downstream of FAM53C loss.

We note, however, that we used specific Thr286 phospho-antibodies, which have been used extensively in the field. Our data in Figure 1 with palbociclib place FAM53C upstream of Cyclin D/CDK4,6. We performed Cyclin D overexpression experiments but RPE-1 cells did not tolerate high expression of Cyclin D1 (T286A mutant) and we have not been able to conduct more ‘genetic’ studies.

At many places, information on statistical tests is missing and SDs are not shown in the plots. For instance, what statistics was used in Fig 4C? Impact of FAM53C on cyclin D phosphorylation does not seem to be significant. In the same experiment, does DYRK1 inhibitor prevent modification of cyclin D?

As discussed above, we removed some of these data and re-focused the manuscript on p53-p21 as a second pathway activated by loss of FAM53C.

Validation of SM13797 compound in terms of specificity to DYRK1 was not performed.

This is an important point. We had cited an abstract from the company (Biosplice) but we agree that providing data is critical. We have now revised the manuscript with a new analysis of the compound’s specificity using kinase assays. These data are shown in Fig. S3F-H.

A fraction of cells in G1 is a very easy readout but it does not measure progression through the G1 phase. Extension of the S phase or G2 delay would indirectly also result in reduction of the G1 fraction. Instead, authors could measure the dynamics of entry to S phase in cells released from a G1 block or from mitotic shake off.

The Reviewer made a good point. As discussed in our response to Reviewer #1, with p53-null RPE-1 cells, we found that cell numbers do not increase in these conditions where we had observed a cell cycle re-entry (Fig. 4E), which was accompanied by apoptotic cell death (Fig. S4I). Thus, cells re-enter the cell cycle but die as they progress through S-phase and G2/M. We note that inhibition of DYRK1A has been shown to decrease expression of G2/M regulators (PMID: 38839871), which may contribute to the inability of cells treated to DYRK1Ai to divide. Because our data in RPE-1 cells showed that p21 knock-down was not sufficient to allow the FAM53C knock-down cells to re-enter the cell cycle, we did not further analyze p21 in HCT-116 cells. These data indicate that G1 entry by flow cytometry will not always translate into proliferation.

Other points:

Fig. 2C, 2D, 2E graphs should begin with 0

We remade these graphs.

Fig. 5D shows that the difference in p21 levels is not significant in FAM53C-KO cells but difference is mentioned in the text.

We replaced the panel by the correct panel; we apologize for this error.

Fig. 6D comparison of datasets of extremely different sizes does not seem to be appropriate

We agree and revised the text. We hope that the Reviewer will agree with us that it is worth showing these data, which are clearly preliminary but provide evidence of a possible role for FAM53C in the brain.

Could there be alternative splicing in mice generating a partially functional protein without exon 4? Did authors confirm that the animal model does not express FAM53C?

We performed RNA sequencing of mouse embryonic fibroblasts derived from control and mutant mice. We clearly identified fewer reads in exon 4 in the knockout cells, and no other obvious change in the transcript (data not shown). However, immunoblot with mouse cells for FAM53C never worked well in our hands. We made sure to add this caveat to the revised manuscript.

__Reviewer #2 (Significance (Required)): __

Main problem of this study is that the advanced experimental models in IPSCs and mice did not confirm the observations in the cell lines and thus the whole manuscript does not hold together. Although I acknowledge the effort the authors invested in these experiments, the data do not contribute to the main conclusion of the paper that FAM53C/DYRK1 regulates G1/S transition.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This paper identifies FAM53C as a novel regulator of cell cycle progression, particularly at the G1/S transition, by inhibiting DYRK1A. Using data from the Cancer Dependency Map, the authors suggest that FAM53C acts upstream of the Cyclin D-CDK4/6-RB axis by inhibiting DYRK1A.

Specifically, their experiments suggest that FAM53C Knockdown induces G1 arrest in cells, reducing proliferation without triggering apoptosis. DYRK1A Inhibition rescues G1 arrest in P53KO cells, suggesting FAM53C normally suppresses DYRK1A activity. Mass Spectrometry and biochemical assays confirm that FAM53C directly interacts with and inhibits DYRK1A. FAM53C Knockout in Human Cortical Organoids and Mice leads to cell cycle defects, growth impairments, and behavioral changes, reinforcing its biological importance.

Strength of the paper:

The study introduces a novel cell cycle control signalling module upstream of CDK4/6 in G1/S regulation which could have significant impact. The identification of FAM53C using a depmap correlation analysis is a nice example of the power of this dataset. The experiments are carried out mostly in a convincing manner and support the conclusions of the manuscript.

Critique:

1) The experiments rely heavily on siRNA transfections without the appropriate controls. There are so many cases of off-target effects of siRNA in the literature, and specifically for a strong phenotype on S-phase as described here, I would expect to see solid results by additional experiments. This is especially important since the ko mice do not show any significant developmental cell cycle phenotypes. Moreover, FAM53C does not show a strong fitness effect in the depmap dataset, suggesting that it is largely non-essential in most cancer cell lines. For this paper to reach publication in a high-standard journal, I would expect that the authors show a rescue of the S-phase phenotype using an siRNA-resistant cDNA, and show similar S-phase defects using an acute knock out approach with lentiviral gRNA/Cas9 delivery.

We thank the Reviewer for this comment. Please refer to the initial response to the three Reviewers, where we discuss our use of single siRNAs and our results in multiple cell lines. Briefly, we can recapitulate the G1 arrest upon FAM53C knock-down using two independent siRNAs in RPE-1 cells. We also observe the same G1 arrest in p53 knockout cells, suggesting it is not due to a non-specific stress response. In addition, the arrest is dependent on RB, which fits with the genetic and biochemical data placing FAM53C upstream of RB, further supporting a specific phenotype. Human cancer cell lines also arrest in G1 upon FAM53C knock-down, not just RPE-1 cells. Finally, we hope the Reviewer will agree with us that compensatory mechanisms are very common in the cell cycle – which may explain the lack of phenotypes in vivo or upon long-term knockout of FAM53C.

2) The S-phase phenotype following FAM53C should be demonstrated in a larger variety of TP53WT and mutant cell lines. Given that this paper introduces a new G1/S control element, I think this is important for credibility. Ideally, this should be done with acute gRNA/Cas9 gene deletion using a lentiviral delivery system; but if the siRNA rescue experiments work and validate an on-target effect, siRNA would be an appropriate alternative.

We now show data with three cancer cell lines (U2OS, A549, and HCT-116 – Fig. S1E,F and Fig. 4F), in addition to our results in RPE-1 cells and in human cortical organoids. We note that the knock-down experiments are complemented by overexpression data (Fig. 1G-I), by genetic data (our original DepMap screen), and our biochemical data (showing direct binding of FAM53C to DYRK1A).

3) The western blot images shown in the MS appear heavily over-processed and saturated (See for example S4B, 4A, B, and E). Perhaps the authors should provide the original un-processed data of the entire gels?

For several of our panels (e.g., 4E and S4B, now panels S3J and S3K)), we used a true “immunoassay” (as indicated in the legend – not an immunoblot), which is much more quantitative and avoids error-prone steps in standard immunoblots (“Western blots”). Briefly, this system was developed by ProteinSimple. It uses capillary transfer of proteins and ELISA-like quantification with up to 6 logs of dynamic range (see their web site https://www.proteinsimple.com/wes.html). The “bands” we show are just a representation of the luminescence signals in capillaries. We made sure to further clarify the figure legends in the revised manuscript.

Data in 4A are also not a western blot but a radiograph.

For immunoblots, we will provide all the source data with uncropped blots with the final submission.

4) A critical experiment for the proposed mechanism is the rescue of the FAM53C S-phase reduction using DYRK1A inhibition shown in Figure 4. The legend here states that the data were extracted from BrdU incorporation assays, but in Figure S4D only the PI histograms are shown, and the S-phase population is not quantified. The authors should show the BrdU scatterplot and quantify the phenotype using the S-phase population in these plots. G1 measurements from PI histograms are not precise enough to allow for conclusions. Also, why are the intensities of the PI peaks so variable in these plots? Compare, for example, the HCT116 upper and lower panels where the siRNA appears to have caused an increase in ploidy.

We apologize for the confusion and we fixed these errors, for most of the analyses, we used PI to measure G1 and S-phase entry. We added relevant flow cytometry plots to supplemental figures (Fig. S1G, H, I, as well as Fig. S4E and S4K, and Fig. S5F).

5) There's an apparent contradiction in how RB deletion rescues the G1 arrest (Figure 2) while p21 seems to maintain the arrest even when DYRK1A is inhibited. Is p21 not induced when FAM53C is depleted in RB ko cells? This should be measured and discussed.

This comment and comments from the two other Reviewers made us reconsider our model. We re-read carefully the Meyer paper and think that DYRK1A activity may be understood when considering levels of both CycD and p21 at the same time in a continuum (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). While our genetic and biochemical data support a role for FAM53C in DYRK1A inhibition, it is obvious that the regulation of cell cycle progression by FAM53C is not exclusively due to this inhibition. As discussed above and below, we noted an upregulation of p21 upon FAM53C knock-down, and activation of p53 and its targets likely contributes significantly to the phenotypes observed. We added new experiments to support this more complex model (Figure 4 and Figure S4, with new model in S4L).

__Reviewer #3 (Significance (Required)): __

In conclusion, I believe that this MS could potentially be important for the cell cycle field and also provide a new target pathway that could be relevant for cancer therapy. However, the paper has quite a few gaps and inconsistencies that need to be addressed with further experiments. My main worry is that the acute depletion phenotypes appear so strong, while the gene is non-essential in mice and shows only a minor fitness effect in the depmap screens. More convincing controls are necessary to rule out experimental artefacts that misguide the interpretation of the results.

We appreciate this comment and hope that the Reviewer will agree it is still important to share our data with the field, even if the phenotypes in mice are modest.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

We would like to thank all the reviewers for their valuable comments and criticisms. We have thoroughly revised the manuscript and the resource to address all the points raised by the reviewers. Below, we provide a point-by-point response for the sake of clarity.

Reviewer #1

__Evidence, reproducibility and clarity __

Summary: This manuscript, "MAVISp: A Modular Structure-Based Framework for Protein Variant Effects," presents a significant new resource for the scientific community, particularly in the interpretation and characterization of genomic variants. The authors have developed a comprehensive and modular computational framework that integrates various structural and biophysical analyses, alongside existing pathogenicity predictors, to provide crucial mechanistic insights into how variants affect protein structure and function. Importantly, MAVISp is open-source and designed to be extensible, facilitating reuse and adaptation by the broader community.

Major comments: - While the manuscript is formally well-structured (with clear Introduction, Results, Conclusions, and Methods sections), I found it challenging to follow in some parts. In particular, the Introduction is relatively short and lacks a deeper discussion of the state-of-the-art in protein variant effect prediction. Several methods are cited but not sufficiently described, as if prior knowledge were assumed. OPTIONAL: Extend the Introduction to better contextualize existing approaches (e.g., AlphaMissense, EVE, ESM-based predictors) and clarify what MAVISp adds compared to each.

We have expanded the introduction on the state-of-the-art of protein variant effects predictors, explaining how MAVISp departs from them.

- The workflow is summarized in Figure 1(b), which is visually informative. However, the narrative description of the pipeline is somewhat fragmented. It would be helpful to describe in more detail the available modules in MAVISp, and which of them are used in the examples provided. Since different use cases highlight different aspects of the pipeline, it would be useful to emphasize what is done step-by-step in each.

We have added a concise, narrative description of the data flow for MAVISp, as well as improved the description of modules in the main text. We will integrate the results section with a more comprehensive description of the available modules, and then clarify in the case studies which modules were applied to achieve specific results.

OPTIONAL: Consider adding a table or a supplementary figure mapping each use case to the corresponding pipeline steps and modules used.

We have added a supplementary table (Table S2) to guide the reader on the modules and workflows applied for each case study

We also added Table S1 to map the toolkit used by MAVISp to collect the data that are imported and aggregated in the webserver for further guidance.

- The text contains numerous acronyms, some of which are not defined upon first use or are only mentioned in passing. This affects readability. OPTIONAL: Define acronyms upon first appearance, and consider moving less critical technical details (e.g., database names or data formats) to the Methods or Supplementary Information. This would greatly enhance readability.

We revised the usage of acronyms following the reviewer’s directions of defying them at first appearance.

• The code and trained models are publicly available, which is excellent. The modular design and use of widely adopted frameworks (PyTorch and PyTorch Geometric) are also strong points. However, the Methods section could benefit from additional detail regarding feature extraction and preprocessing steps, especially the structural features derived from AlphaFold2 models. OPTIONAL: Include a schematic or a table summarizing all feature types, their dimensionality, and how they are computed.

We thank the reviewer for noticing and praising the availability of the tools of MAVISp. Our MAVISp framework utilizes methods and scores that incorporate machine learning features (such as EVE or RaSP), but does not employ machine learning itself. Specifically, we do not use PyTorch and do not utilize features in a machine learning sense. We do extract some information from the AlphaFold2 models that we use (such as the pLDDT score and their secondary structure content, as calculated by DSSP), and those are available in the MAVISp aggregated csv files for each protein entry and detailed in the Documentation section of the MAVISp website.

• The section on transcription factors is relatively underdeveloped compared to other use cases and lacks sufficient depth or demonstration of its practical utility. OPTIONAL: Consider either expanding this section with additional validation or removing/postponing it to a future manuscript, as it currently seems preliminary.

We have removed this section and included a mention in the conclusions as part of the future directions.

Minor comments: - Most relevant recent works are cited, including EVE, ESM-1v, and AlphaFold-based predictors. However, recent methods like AlphaMissense (Cheng et al., 2023) could be discussed more thoroughly in the comparison.

We have revised the introduction to accommodate the proper space for this comparison.

• Figures are generally clear, though some (e.g., performance barplots) are quite dense. Consider enlarging font sizes and annotating key results directly on the plots.

We have revised Figure 2 and presented only one case study to simplify its readability. We have also changed Figure 3, whereas retained the other previous figures since they seemed less problematic.

• Minor typographic errors are present. A careful proofreading is highly recommended. Below are some of the issues I identified: Page 3, line 46: "MAVISp perform" -> "MAVISp performs" Page 3, line 56: "automatically as embedded" -> "automatically embedded" Page 3, line 57: "along with to enhance" -> unclear; please revise Page 4, line 96: "web app interfaces with the database and present" -> "presents" Page 6, line 210: "to investigate wheatear" -> "whether" Page 6, lines 215-216: "We have in queue for processing with MAVISp proteins from datasets relevant to the benchmark of the PTM module." -> unclear sentence; please clarify Page 15, line 446: "Both the approaches" -> "Both approaches" Page 20, line 704: "advantage of multi-core system" -> "multi-core systems"

We have done a proofreading of the entire article, including the points above

Significance

General assessment: the strongest aspects of the study are the modularity, open-source implementation, and the integration of structural information through graph neural networks. MAVISp appears to be one of the few publicly available frameworks that can easily incorporate AlphaFold2-based features in a flexible way, lowering the barrier for developing custom predictors. Its reproducibility and transparency make it a valuable resource. However, while the technical foundation is solid and the effort substantial, the scientific narrative and presentation could be significantly improved. The manuscript is dense and hard to follow in places, with a heavy use of acronyms and insufficient explanation of key design choices. Improving the descriptive clarity, especially in the early sections, would greatly enhance the impact of this work.

Advance

to the best of my knowledge, this is one of the first modular platforms for protein variant effect prediction that integrates structural data from AlphaFold2 with bioinformatic annotations and even clinical data in an extensible fashion. While similar efforts exist (e.g., ESMfold, AlphaMissense), MAVISp distinguishes itself through openness and design for reusability. The novelty is primarily technical and practical rather than conceptual.

Audience

this study will be of strong interest to researchers in computational biology, structural bioinformatics, and genomics, particularly those developing variant effect predictors or analyzing the impact of mutations in clinical or functional genomics contexts. The audience is primarily specialized, but the open-source nature of the tool may diffuse its use among more applied or translational users, including those working in precision medicine or protein engineering.

Reviewer expertise: my expertise is in computational structural biology, molecular modeling, and (rather weak) machine learning applications in bioinformatics. I am familiar with graph-based representations of proteins, AlphaFold2, and variant effects based on Molecular Dynamics simulations. I do not have any direct expertise in clinical variant annotation pipelines.

Reviewer #2

__Evidence, reproducibility and clarity __

Summary: The authors present a pipeline and platform, MAVISp, for aggregating, displaying and analysis of variant effects with a focus on reclassification of variants of uncertain clinical significance and uncovering the molecular mechanisms underlying the mutations.

Major comments: - On testing the platform, I was unable to look-up a specific variant in ADCK1 (rs200211943, R115Q). I found that despite stating that the mapped refseq ID was NP_001136017 in the HGVSp column, it was actually mapped to the canonical UniProt sequence (Q86TW2-1). NP_001136017 actually maps to Q86TW2-3, which is missing residues 74-148 compared to the -1 isoform. The Uniprot canonical sequence has no exact RefSeq mapping, so the HGVSp column is incorrect in this instance. This mapping issue may also affect other proteins and result in incorrect HGVSp identifiers for variants.

We would like to thank the reviewer for pointing out these inconsistencies. We have revised all the entries and corrected them. If needed, the history of the cases that have been corrected can be found in the closed issues of the GitHub repository that we use for communication between biocurators and data managers (https://github.com/ELELAB/mavisp_data_collection). We have also revised the protocol we follow in this regard and the MAVISp toolkit to include better support for isoform matching in our pipelines for future entries, as well as for the revision/monitoring of existing ones, as detailed in the Method Section. In particular, we introduced a tool, uniprot2refseq, which aids the biocurator in identifying the correct match in terms of sequence length and sequence identity between RefSeq and UniProt. More details are included in the Method Section of the paper. The two relevant scripts for this step are available at: https://github.com/ELELAB/mavisp_accessory_tools/

- The paper lacks a section on how to properly interpret the results of the MAVISp platform (the case-studies are helpful, but don't lay down any global rules for interpreting the results). For example: How should a variant with conflicts between the variant impact predictors be interpreted? Are specific indicators considered more 'reliable' than others?

We have added a section in Results to clarify how to interpret results from MAVISp in the most common use cases.

• In the Methods section, GEMME is stated as being rank-normalised with 0.5 as a threshold for damaging variants. On checking the data downloaded from the site, GEMME was not rank-normalised but rather min-max normalised. Furthermore, Supplementary text S4 conflicts with the methods section over how GEMME scores are classified, S4 states that a raw-value threshold of -3 is used.

We thank the reviewer for spotting this inconsistency. This part in the main text was left over from a previous and preliminary version of the pre-print, we have revised the main text. Supplementary Text S4 includes the correct reference for the value in light of the benchmarking therewithin.

• Note. This is a major comment as one of the claims is that the associated web-tool is user-friendly. While functional, the web app is very awkward to use for analysis on any more than a few variants at once. The fixed window size of the protein table necessitates excessive scrolling to reach your protein-of-interest. This will also get worse as more proteins are added. Suggestion: add a search/filter bar. The same applies to the dataset window.

We have changed the structure of the webserver in such a way that now the whole website opens as its own separate window, instead of being confined within the size permitted by the website at DTU. This solves the fixed window size issue. Hopefully, this will improve the user experience.

We have refactored the web app by adding filtering functionality, both for the main protein table (that can now be filtered by UniProt AC, gene name or RefSeq ID) and the mutations table. Doing this required a general overhaul of the table infrastructure (we changed the underlying engine that renders the tables).

• You are unable to copy anything out of the tables.
• Hyperlinks in the tables only seem to work if you open them in a new tab or window.

The table overhauls fixed both of these issues

• All entries in the reference column point to the MAVISp preprint even when data from other sources is displayed (e.g. MAVE studies).

We clarified the meaning of the reference column in the Documentation on the MAVISp website, as we realized it had confused the reviewer. The reference column is meant to cite the papers where the computationally-generated MAVISp data are used, not external sources. Since we also have the experimental data module in the most recent release, we have also refactored the MAVISp website by adding a “Datasets and metadata” page, which details metadata for key modules. These include references to data from external sources that we include in MAVISp on a case-by-case basis (for example the results of a MAVE experiment). Additionally, we have verified that the papers using MAVISp data are updated in https://elelab.gitbook.io/mavisp/overview/publications-that-used-mavisp-data and in the csv file of the interested proteins.

Here below the current references that have been included in terms of publications using MAVISp data:

SMPD1

ASM variants in the spotlight: A structure-based atlas for unraveling pathogenic mechanisms in lysosomal acid sphingomyelinase

Biochim Biophys Acta Mol Basis Dis

38782304

https://doi.org/10.1016/j.bbadis.2024.167260

TRAP1

Point mutations of the mitochondrial chaperone TRAP1 affect its functions and pro-neoplastic activity

Cell Death & Disease

40074754

https://doi.org/10.1038/s41419-025-07467-6

BRCA2

Saturation genome editing-based clinical classification of BRCA2 variants

Nature

39779848

0.1038/s41586-024-08349-1

TP53, GRIN2A, CBFB, CALR, EGFR

TRAP1 S-nitrosylation as a model of population-shift mechanism to study the effects of nitric oxide on redox-sensitive oncoproteins

Cell Death & Disease

37085483

10.1038/s41419-023-05780-6

KIF5A, CFAP410, PILRA, CYP2R1

Computational analysis of five neurodegenerative diseases reveals shared and specific genetic loci

Computational and Structural Biotechnology Journal

38022694

https://doi.org/10.1016/j.csbj.2023.10.031

KRAS

Combining evolution and protein language models for an interpretable cancer driver mutation prediction with D2Deep

Brief Bioinform

39708841

https://doi.org/10.1093/bib/bbae664

OPTN

Decoding phospho-regulation and flanking regions in autophagy-associated short linear motifs

Communications Biology

40835742

10.1038/s42003-025-08399-9

DLG4,GRB2,SMPD1

Deciphering long-range effects of mutations: an integrated approach using elastic network models and protein structure networks

JMB

40738203

doi: 10.1016/j.jmb.2025.169359

Entering multiple mutants in the "mutations to be displayed" window is time-consuming for more than a handful of mutants. Suggestion: Add a box where multiple mutants can be pasted in at once from an external document.

During the table overhaul, we have revised the user interface to add a text box that allows free copy-pasting of mutation lists. While we understand having a single input box would have been ideal, the former selection interface (which is also still available) doesn’t allow copy-paste. This is a known limitation in Streamlit.

Minor comments

• Grammar. I appreciate that this manuscript may have been compiled by a non-native English speaker, but I would be remiss not to point out that there are numerous grammar errors throughout, usually sentence order issues or non-pluralisation. The meaning of the authors is mostly clear, but I recommend very thoroughly proof-reading the final version.

We have done proofreading on the final version of the manuscript

• There are numerous proteins that I know have high-quality MAVE datasets that are absent in the database e.g. BRCA1, HRAS and PPARG.

Yes, we are aware of this. It is far from trivial to properly import the datasets from multiplex assays. They often need to be treated on a case-by-case basis. We are in the process of carefully compiling locally all the MAVE data before releasing it within the public version of the database, so this is why they are missing. We are giving priorities to the ones that can be correlated with our predictions on changes in structural stability and then we will also cover the rest of the datasets handling them in batches. Having said this, we have checked the dataset for BRCA1, HRAS, and PPARG. We have imported the ones for PPARG and BRCA1 from ProtGym, referring to the studies published in 10.1038/ng.3700 and 10.1038/s41586-018-0461-z, respectively. Whereas for HRAS, checking in details both the available data and literature, while we did identify a suitable dataset (10.7554/eLife.27810), we struggled to understand what a sensible cut-off for discriminating between pathogenic and non-pathogenic variants would be, and so ended up not including it in the MAVISp dataset for now. We will contact the authors to clarify which thresholds to apply before importing the data.

• Checking one of the existing MAVE datasets (KRAS), I found that the variants were annotated as damaging, neutral or given a positive score (these appear to stand-in for gain-of-function variants). For better correspondence with the other columns, those with positive scores could be labelled as 'ambiguous' or 'uncertain'.

In the KRAS case study presented in MAVISP, we utilized the protein abundance dataset reported in (http://dx.doi.org/10.1038/s41586-023-06954-0) and made available in the ProteinGym repository (specifically referenced at https://github.com/OATML-Markslab/ProteinGym/blob/main/reference_files/DMS_substitutions.csv#L153). We adopted the precalculated thresholds as provided by the ProteinGym authors. In this regard, we are not really sure the reviewer is referring to this dataset or another one on KRAS.

• Numerous thresholds are defined for stabilizing / destabilizing / neutral variants in both the STABILITY and the LOCAL_INTERACTION modules. How were these thresholds determined? I note that (PMC9795540) uses a ΔΔG threshold of 1/-1 for defining stabilizing and destabilizing variants, which is relatively standard (though they also say that 2-3 would likely be better for pinpointing pathogenic variants).

We improved the description of our classification strategies for both modules in the Documentation page of our website. Also, we explained more clearly the possible sources of ‘uncertain’ annotations for the two modules in both the web app (Documentation page) and main text. Briefly, in the STABILITY module, we consider FoldX and either Rosetta or RaSP to achieve a final classification. We first classify one and the other independently, according to the following strategy:

If DDG ≥ 3, the mutation is Destabilizing If DDG ≤ −3, the mutation is Stabilizing If −2 We then compare the classifications obtained by the two methods: if they agree, then that is the final classification, if they disagree, then the final classification is Uncertain. The thresholds were selected based on a previous study, in which variants with changes in stability below 3 kcal/mol were not featuring a markedly different abundance at cellular level [10.1371/journal.pgen.1006739, 10.7554/eLife.49138]

Regarding the LOCAL_INTERACTION module, it works similarly as for the Stability module, in that Rosetta and FoldX are considered independently, and an implicit classification is performed for each, according to the rules (values in kcal/mol)

If DDG > 1, the mutation is Destabilizing. If DDG Each mutation is therefore classified for both methods. If the methods agree (i.e., if they classify the mutation in the same way), their consensus is the final classification for the mutation; if they do not agree, the final classification will be Uncertain.

If a mutation does not have an associated free energy value, the relative solvent accessible area is used to classify it: if SAS > 20%, the mutation is classified as Uncertain, otherwise it is not classified.

Thresholds here were selected according to best practices followed by the tool authors and more in general in the literature, as the reviewer also noticed.

• "Overall, with the examples in this section, we illustrate different applications of the MAVISp results, spanning from benchmarking purposes, using the experimental data to link predicted functional effects with structural mechanisms or using experimental data to validate the predictions from the MAVISp modules."

The last of these points is not an application of MAVISp, but rather a way in which external data can help validate MAVISp results. Furthermore, none of the examples given demonstrate an application in benchmarking (what is being benchmarked?).

We have revised the statements to avoid this confusion in the reader.

• Transcription factors section. This section describes an intended future expansion to MAVISp, not a current feature, and presents no results. As such, it should be moved to the conclusions/future directions section.

We have removed this section and included a mention in the conclusions as part of the future directions.

• Figures. The dot-plots generated by the web app, and in Figures 4, 5 and 6 have 2 legends. After looking at a few, it is clear that the lower legend refers to the colour of the variant on the X-axis - most likely referencing the ClinVar effect category. This is not, however, made clear either on the figures or in the app.

The reviewer’s interpretation on the second legend is correct - it does refer to the ClinVar classification. Nonetheless, we understand the positioning of the legend makes understanding what the legend refers to not obvious. We also revised the captions of the figures in the main text. On the web app, we have changed the location of the figure legend for the ClinVar effect category and added a label to make it clear what the classification refers to.

• "We identified ten variants reported in ClinVar as VUS (E102K, H86D, T29I, V91I, P2R, L44P, L44F, D56G, R11L, and E25Q, Fig.5a)" E25Q is benign in ClinVar and has had that status since first submitted.

We have corrected this in the text and the statements related to it.

Significance

Platforms that aggregate predictors of variant effect are not a new concept, for example dbNSFP is a database of SNV predictions from variant effect predictors and conservation predictors over the whole human proteome. Predictors such as CADD and PolyPhen-2 will often provide a summary of other predictions (their features) when using their platforms. MAVISp's unique angle on the problem is in the inclusion of diverse predictors from each of its different moules, giving a much wider perspective on variants and potentially allowing the user to identify the mechanistic cause of pathogenicity. The visualisation aspect of the web app is also a useful addition, although the user interface is somewhat awkward. Potentially the most valuable aspect of this study is the associated gitbook resource containing reports from biocurators for proteins that link relevant literature and analyse ClinVar variants. Unfortunately, these are only currently available for a small minority of the total proteins in the database with such reports. For improvement, I think that the paper should focus more on the precise utility of the web app / gitbook reports and how to interpret the results rather than going into detail about the underlying pipeline.

We appreciate the interest in the gitbook resource that we also see as very valuable and one of the strengths of our work. We have now implemented a new strategy based on a Python script introduced in the mavisp toolkit to generate a template Markdown file of the report that can be further customized and imported into GitBook directly (​​https://github.com/ELELAB/mavisp_accessory_tools/). This should allow us to streamline the production of more reports. We are currently assigning proteins in batches for reporting to biocurator through the mavisp_data_collection GitHub to expand their coverage. Also, we revised the text and added a section on the interpretation of results from MAVISp. with a focus on the utility of the web-app and reports.

In terms of audience, the fast look-up and visualisation aspects of the web-platform are likely to be of interest to clinicians in the interpretation of variants of unknown clinical significance. The ability to download the fully processed dataset on a per-protein database would be of more interest to researchers focusing on specific proteins or those taking a broader view over multiple proteins (although a facility to download the whole database would be more useful for this final group).

While our website only displays the dataset per protein, the whole dataset, including all the MAVISp entries, is available at our OSF repository (https://osf.io/ufpzm/), which is cited in the paper and linked on the MAVISp website. We have further modified the MAVISp database to add a link to the repository in the modes page, so that it is more visible.

My expertise. - I am a protein bioinformatician with a background in variant effect prediction and large-scale data analysis.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Evidence, reproducibility and clarity:

Summary:

The authors present MAVISp, a tool for viewing protein variants heavily based on protein structure information. The authors have done a very impressive amount of curation on various protein targets, and should be commended for their efforts. The tool includes a diverse array of experimental, clinical, and computational data sources that provides value to potential users interested in a given target.

Major comments:

Unfortunately I was not able to get the website to work correctly. When selecting a protein target in simple mode, I was greeted with a completely blank page in the app window. In ensemble mode, there was no transition away from the list of targets at all. I'm using Firefox 140.0.2 (64-bit) on Ubuntu 22.04. I would like to explore the data myself and provide feedback on the user experience and utility.

We have tried reproducing the issue mentioned by the reviewer, using the exact same Ubuntu and Firefox versions, but unfortunately failed to produce it. The website worked fine for us under such an environment. The issue experienced by the reviewer may have been due to either a temporary issue with the web server or a problem with the specific browser environment they were working in, which we are unable to reproduce. It would be useful to know the date that this happened to verify if it was a downtime on the DTU IT services side that made the webserver inaccessible.

I have some serious concerns about the sustainability of the project and think that additional clarifications in the text could help. Currently is there a way to easily update a dataset to add, remove, or update a component (for example, if a new predictor is published, an error is found in a predictor dataset, or a predictor is updated)? If it requires a new round of manual curation for each protein to do this, I am worried that this will not scale and will leave the project with many out of date entries. The diversity of software tools (e.g., three different pipeline frameworks) also seems quite challenging to maintain.

We appreciate the reviewer’s concerns about long-term sustainability. It is a fair point that we consider within our steering group, who oversee and plans the activities and meet monthly. Adding entries to MAVISp is moving more and more towards automation as we grow. We aim to minimize the manual work where applicable. Still, an expert-based intervention is really needed in some of the steps, and we do not want to renounce it. We intend to keep working on MAVISp to make the process of adding and updating entries as automated as possible, and to streamline the process when manual intervention is necessary. From the point of view of the biocurators, they have three core workflows to use for the default modules, which also automatically cover the source of annotations. We are currently working to streamline the procedures behind LOCAL_INTERACTION, which is the most challenging one. On the data manager and maintainers' side, we have workflows and protocols that help us in terms of automation, quality control, etc, and we keep working to improve them. Among these, we have workflows to use for the old entries updates. As an example, the update of erroneously attributed RefSeq data (pointed out by reviewer 2) took us only one week overall (from assigning revisions and importing to the database) because we have a reduced version of Snakemake for automation that can act on only the affected modules. Also, another point is that we have streamlined the generation of the templates for the gitbook reports (see also answer to reviewer 2).

The update of old entries is planned and made regularly. We also deposit the old datasets on OSF for transparency, in case someone needs to navigate and explore the changes. We have activities planned between May and August every year to update the old entries in relation to changes of protocols in the modules, updates in the core databases that we interact with (COSMIC, Clinvar etc). In case of major changes, the activities for updates continue in the Fall. Other revisions can happen outside these time windows if an entry is needed or a specific research project and needs updates too.

Furthermore, the community of people contributing to MAVISp as biocurators or developers is growing and we have scientists contributing from other groups in relation to their research interest. We envision that for this resource to scale up, our team cannot be the only one producing data and depositing it to the database. To facilitate this we launched a pilot for a training event online (see Event page on the website) and we will repeat it once per year. We also organize regular meetings with all the active curators and developers to plan the activities in a sustainable manner and address the challenges we encounter.

As stated in the manuscript, currently with the team of people involved, automatization and resources that we have gathered around this initiative we can provide updates to the public database every third month and we have been regularly satisfied with them. Additionally, we are capable of processing from 20 to 40 proteins every month depending also on the needs of revision or expansion of analyses on existing proteins. We also depend on these data for our own research projects and we are fully committed to it.

Additionally, we are planning future activities in these directions to improve scale up and sustainability:

• Streamlining manual steps so that they are as convenient as fast as possible for our curators, e.g. by providing custom pages on the MAVISp website
• Streamline and automatize the generation of useful output, for instance the reports, by using a combination of simple automation and large language models
• Implement ways to share our software and scripts with third parties, for instance by providing ready made (or close to) containers or virtual machines
• For a future version 2 if the database grows in a direction that is not compatible with Streamlit, the web data science framework we are currently using, we will rewrite the website using a framework that would allow better flexibility and performance, for instance using Django and a proper database backend. On the same theme, according to the GitHub repository, the program relies on Python 3.9, which reaches end of life in October 2025. It has been tested against Ubuntu 18.04, which left standard support in May 2023. The authors should update the software to more modern versions of Python to promote the long-term health and maintainability of the project.

We thank the reviewer for this comment - we are aware of the upcoming EOL of Python 3.9. We tested MAVISp, both software package and web server, using Python 3.10 (which is the minimum supported version going forward) and Python 3.13 (which is the latest stable release at the time of writing) and updated the instructions in the README file on the MAVISp GitHub repository accordingly.

We plan on keeping track of Python and library versions during our testing and updating them when necessary. In the future, we also plan to deploy Continuous Integration with automated testing for our repository, making this process easier and more standardized.

I appreciate that the authors have made their code and data available. These artifacts should also be versioned and archived in a service like Zenodo, so that researchers who rely on or want to refer to specific versions can do so in their own future publications.

Since 2024, we have been reporting all previous versions of the dataset on OSF, the repository linked to the MAVISp website, at https://osf.io/ufpzm/files/osfstorage (folder: previous_releases). We prefer to keep everything under OSF, as we also use it to deposit, for example, the MD trajectory data.

Additionally, in this GitHub page that we use as a space to interact between biocurators, developers, and data managers within the MAVISp community, we also report all the changes in the NEWS space: https://github.com/ELELAB/mavisp_data_collection

Finally, the individual tools are all available in our GitHub repository, where version control is in place (see Table S1, where we now mapped all the resources used in the framework)

In the introduction of the paper, the authors conflate the clinical challenges of variant classification with evidence generation and it's quite muddled together. They should strongly consider splitting the first paragraph into two paragraphs - one about challenges in variant classification/clinical genetics/precision oncology and another about variant effect prediction and experimental methods. The authors should also note that they are many predictors other than AlphaMissense, and may want to cite the ClinGen recommendations (PMID: 36413997) in the intro instead.

We revised the introduction in light of these suggestions. We have split the paragraph as recommended and added a longer second paragraph about VEPs and using structural data in the context of VEPs. We have also added the citation that the reviewer kindly recommended.

Also in the introduction on lines 21-22 the authors assert that "a mechanistic understanding of variant effects is essential knowledge" for a variety of clinical outcomes. While this is nice, it is clearly not the case as we can classify variants according to the ACMG/AMP guidelines without any notion of specific mechanism (for example, by combining population frequency data, in silico predictor data, and functional assay data). The authors should revise the statement so that it's clear that mechanistic understanding is a worthy aspiration rather than a prerequisite.

We revised the statement in light of this comment from the reviewer

In the structural analysis section (page 5, lines 154-155 and elsewhere), the authors define cutoffs with convenient round numbers. Is there a citation for these values or were these arbitrarily chosen by the authors? I would have liked to see some justification that these assignments are reasonable. Also there seems to be an error in the text where values between -2 and -3 kcal/mol are not assigned to a bin (I assume they should also be uncertain). There are other similar seemingly-arbitrary cutoffs later in the section that should also be explained.

We have revised the text making the two intervals explicit, for better clarity.

On page 9, lines 294-298 the authors talk about using the PTEN data from ProteinGym, rather than the actual cutoffs from the paper. They get to the latter later on, but I'm not sure why this isn't first? The ProteinGym cutoffs are somewhat arbitrarily based on the median rather than expert evaluation of the dataset, and I'm not sure why it's even worth mentioning them when proper classifications are available. Regarding PTEN, it would be quite interesting to see a comparison of the VAMP-seq PTEN data and the Mighell phosphatase assay, which is cited on page 9 line 288 but is not actually a VAMP-seq dataset. I think this section could be interesting but it requires some additional attention.

We have included the data from Mighell’s phosphatase assay as provided by MAVEdb in the MAVISp database, within the experimental_data module for PTEN, and we have revised the case study, including them and explaining better the decision of supporting both the ProteinGym and MAVEdb classification in MAVISp (when available). See revised Figure3, Table 1 and corresponding text.

The authors mention "pathogenicity predictors" and otherwise use pathogenicity incorrectly throughout the manuscript. Pathogenicity is a classification for a variant after it has been curated according to a framework like the ACMG/AMP guidelines (Richards 2015 and amendments). A single tool cannot predict or assign pathogenicity - the AlphaMissense paper was wrong to use this nomenclature and these authors should not compound this mistake. These predictors should be referred to as "variant effect predictors" or similar, and they are able to produce evidence towards pathogenicity or benignity but not make pathogenicity calls themselves. For example, in Figure 4e, the terms "pathogenic" and "benign" should only be used here if these are the classifications the authors have derived from ClinVar or a similar source of clinically classified variants.

The reviewer is correct, we have revised the terminology we used in the manuscript and refers to VEPs (Variant Effect Predictors)

Minor comments:

The target selection table on the website needs some kind of text filtering option. It's very tedious to have to find a protein by scrolling through the table rather than typing in the symbol. This will only get worse as more datasets are added.

We have revised the website, adding a filtering option. In detail, we have refactored the web app by adding filtering functionality, both for the main protein table (that can now be filtered by UniProt AC, gene name, or RefSeq ID) and the mutations table. Doing this required a general overhaul of the table infrastructure (we changed the underlying engine that renders the tables).

The data sources listed on the data usage section of the website are not concordant with what is in the paper. For example, MaveDB is not listed.

We have revised and updated the data sources on the website, adding a metadata section with relevant information, including MaveDB references where applicable.

Figure 2 is somewhat confusing, as it partially interleaves results from two different proteins. This would be nicer as two separate figures, one on each protein, or just of a single protein.

As suggested by the reviewer, we have now revised the figure and corresponding legends and text, focusing only on one of the two proteins.

Figure 3 panel b is distractingly large and I wonder if the authors could do a little bit more with this visualization.

We have revised Figure 3 to solve these issues and integrating new data from the comparison with the phosphatase assay

Capitalization is inconsistent throughout the manuscript. For example, page 9 line 288 refers to VampSEQ instead of VAMP-seq (although this is correct elsewhere). MaveDB is referred to as MAVEdb or MAVEDB in various places. AlphaMissense is referred to as Alphamissense in the Figure 5 legend. The authors should make a careful pass through the manuscript to address this kind of issues.

We have carefully proofread the paper for these inconsistencies

MaveDB has a more recent paper (PMID: 39838450) that should be cited instead of/in addition to Esposito et al.

We have added the reference that the reviewer recommended

On page 11, lines 338-339 the authors mention some interesting proteins including BLC2, which has base editor data available (PMID: 35288574). Are there plans to incorporate this type of functional assay data into MAVISp?

The assay mentioned in the paper refers to an experimental setup designed to investigate mutations that may confer resistance to the drug venetoclax. We started the first steps to implement a MAVISp module aimed at evaluating the impact of mutations on drug binding using alchemical free energy perturbations (ensemble mode) but we are far from having it complete. We expect to import these data when the module will be finalized since they can be used to benchmark it and BCL2 is one of the proteins that we are using to develop and test the new module.

Reviewer #3 (Significance (Required)):

Significance:

General assessment:

This is a nice resource and the authors have clearly put a lot of effort in. They should be celebrated for their achievments in curating the diverse datasets, and the GitBooks are a nice approach. However, I wasn't able to get the website to work and I have raised several issues with the paper itself that I think should be addressed.

Advance:

New ways to explore and integrate complex data like protein structures and variant effects are always interesting and welcome. I appreciate the effort towards manual curation of datasets. This work is very similar in theme to existing tools like Genomics 2 Proteins portal (PMID: 38260256) and ProtVar (PMID: 38769064). Unfortunately as I wasn't able to use the site I can't comment further on MAVISp's position in the landscape.

We have expanded the conclusions section to add a comparison and cite previously published work, and linked to a review we published last year that frames MAVISp in the context of computational frameworks for the prediction of variant effects. In brief, the Genomics 2 Proteins portal (G2P) includes data from several sources, including some overlapping with MAVISp such as Phosphosite or MAVEdb, as well as features calculated on the protein structure. ProtVar also aggregates mutations from different sources and includes both variant effect predictors and predictions of changes in stability upon mutation, as well as predictions of complex structures. These approaches are only partially overlapping with MAVISp. G2P is primarily focused on structural and other annotations of the effect of a mutation; it doesn’t include features about changes of stability, binding, or long-range effects, and doesn’t attempt to classify the impact of a mutation according to its measurements. It also doesn’t include information on protein dynamics. Similarly, ProtVar does include information on binding free energies, long effects, or dynamical information.

Audience:

MAVISp could appeal to a diverse group of researchers who are interested in the biology or biochemistry of proteins that are included, or are interested in protein variants in general either from a computational/machine learning perspective or from a genetics/genomics perspective.

My expertise:

I am an expert in high-throughput functional genomics experiments and am an experienced computational biologist with software engineering experience.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

Summary:

The authors present MAVISp, a tool for viewing protein variants heavily based on protein structure information. The authors have done a very impressive amount of curation on various protein targets, and should be commended for their efforts. The tool includes a diverse array of experimental, clinical, and computational data sources that provides value to potential users interested in a given target.

Major comments:

Unfortunately I was not able to get the website to work properly. When selecting a protein target in simple mode, I was greeted with a completely blank page in the app window, and in ensemble mode, there was no transition away from the list of targets at all. I'm using Firefox 140.0.2 (64-bit) on Ubuntu 22.04. I would have liked to be able to explore the data myself and provide feedback on the user experience and utility.

I have some serious concerns about the sustainability of the project and think that additional clarifications in the text could help. Currently is there a way to easily update a dataset to add, remove, or update a component (for example, if a new predictor is published, an error is found in a predictor dataset, or a predictor is updated)? If it requires a new round of manual curation for each protein to do this, I am worried that this will not scale and will leave the project with many out of date entries. The diversity of software tools (e.g., three different pipeline frameworks) also seems quite challenging to maintain.

On the same theme, according to the GitHub repository, the program relies on Python 3.9, which reaches end of life in October 2025. It has been tested against Ubuntu 18.04, which left standard support in May 2023. The authors should update the software to more modern versions of Python to promote the long-term health and maintainability of the project.

I appreciate that the authors have made their code and data available. These artifacts should also be versioned and archived in a service like Zenodo, so that researchers who rely on or want to refer to specific versions can do so in their own future publications.

In the introduction of the paper, the authors conflate the clinical challenges of variant classification with evidence generation and it's quite muddled together. The y should strongly consider splitting the first paragraph into two paragraphs - one about challenges in variant classification/clinical genetics/precision oncology and another about variant effect prediction and experimental methods. The authors should also note that they are many predictors other than AlphaMissense, and may want to cite the ClinGen recommendations (PMID: 36413997) in the intro instead.

Also in the introduction on lines 21-22 the authors assert that "a mechanistic understanding of variant effects is essential knowledge" for a variety of clinical outcomes. While this is nice, it is clearly not the case as we are able to classify variants according to the ACMG/AMP guidelines without any notion of specific mechanism (for example, by combining population frequency data, in silico predictor data, and functional assay data). The authors should revise the statement so that it's clear that mechanistic understanding is a worthy aspiration rather than a prerequisite.

In the structural analysis section (page 5, lines 154-155 and elsewhere), the authors define cutoffs with convenient round numbers. Is there a citation for these values or were these arbitrarily chosen by the authors? I would have liked to see some justification that these assignments are reasonable. Also there seems to be an error in the text where values between -2 and -3 kcal/mol are not assigned to a bin (I assume they should also be uncertain). There are other similar seemingly-arbitrary cutoffs later in the section that should also be explained.

On page 9, lines 294-298 the authors talk about using the PTEN data from ProteinGym, rather than the actual cutoffs from the paper. They get to the latter later on, but I'm not sure why this isn't first? The ProteinGym cutoffs are somewhat arbitrarily based on the median rather than expert evaluation of the dataset and I'm not sure why it's even worth mentioning them when proper classifications are available. Regarding PTEN, it would be quite interesting to see a comparison of the VAMP-seq PTEN data and the Mighell phosphatase assay, which is cited on page 9 line 288 but is not actually a VAMP-seq dataset. I think this section could be interesting but it requires some additional attention.

The authors mention "pathogenicity predictors" and otherwise use pathogenicity incorrectly throughout the manuscript. Pathogenicity is a classification for a variant after it has been curated according to a framework like the ACMG/AMP guidelines (Richards 2015 and amendments). A single tool cannot predict or assign pathogenicity - the AlphaMissense paper was wrong to use this nomenclature and these authors should not compound this mistake. These predictors should be referred to as "variant effect predictors" or similar, and they are able to produce evidence towards pathogenicity or benignity but not make pathogenicity calls themselves. For example, in Figure 4e, the terms "pathogenic" and "benign" should only be used here if these are the classifications the authors have derived from ClinVar or a similar source of clinically classified variants.

Minor comments:

The target selection table on the website needs some kind of text filtering option. It's very tedious to have to find a protein by scrolling through the table rather than typing in the symbol. This will only get worse as more datasets are added.

The data sources listed on the data usage section of the website are not concordant with what is in the paper. For example, MaveDB is not listed.

I found Figure 2 to be a bit confusing in that it partially interleaves results from two different proteins. I think this would be nicer as two separate figures, one on each protein, or just of a single protein.

Figure 3 panel b is distractingly large and I wonder if the authors could do a little bit more with this visualization.

Capitalization is inconsistent throughout the manuscript. For example, page 9 line 288 refers to VampSEQ instead of VAMP-seq (although this is correct elsewhere). MaveDB is referred to as MAVEdb or MAVEDB in various places. AlphaMissense is referred to as Alphamissense in the Figure 5 legend. The authors should make a careful pass through the manuscript to address this kind of issues.

MaveDB has a more recent paper (PMID: 39838450) that should be cited instead of/in addition to Esposito et al.

On page 11, lines 338-339 the authors mention some interesting proteins including BLC2, which has base editor data available (PMID: 35288574). Are there plans to incorporate this type of functional assay data into MAVISp?

Significance

General assessment:

This is a nice resource and the authors have clearly put a lot of effort in. They should be celebrated for their achievments in curating the diverse datasets, and the GitBooks are a nice approach. However, I wasn't able to get the website to work and I have raised several issues with the paper itself that I think should be addressed.

Advance:

New ways to explore and integrate complex data like protein structures and variant effects are always interesting and welcome. I appreciate the effort towards manual curation of datasets. This work is very similar in theme to existing tools like Genomics 2 Proteins portal (PMID: 38260256) and ProtVar (PMID: 38769064). Unfortunately as I wasn't able to use the site I can't comment further on MAVISp's position in the landscape.

Audience:

MAVISp could appeal to a diverse group of researchers who are interested in the biology or biochemistry of proteins that are included, or are interested in protein variants in general either from a computational/machine learning perspective or from a genetics/genomics perspective.

My expertise:

I am an expert in high-throughput functional genomics experiments and am an experienced computational biologist with software engineering experience.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary:

The authors present a pipeline and platform, MAVISp, for aggregating, displaying and analysis of variant effects with a focus on reclassification of variants of uncertain clinical significance and uncovering the molecular mechanisms underlying the mutations.

Major comments:

• On testing the platform, I was unable to look-up a specific variant in ADCK1 (rs200211943, R115Q). I found that despite stating that the mapped refseq ID was NP_001136017 in the HGVSp column, it was actually mapped to the canonical UniProt sequence (Q86TW2-1). NP_001136017 actually maps to Q86TW2-3, which is missing residues 74-148 compared to the -1 isoform. The Uniprot canonical sequence has no exact RefSeq mapping, so the HGVSp column is incorrect in this instance. This mapping issue may also affect other proteins and result in incorrect HGVSp identifiers for variants.
• The paper lacks a section on how to properly interpret the results of the MAVISp platform (the case-studies are useful, but don't lay down any global rules for interpreting the results). For example: How should a variant with conflicts between the variant impact predictors be interpreted? Are certain indicators considered more 'reliable' than others?
• In the Methods section, GEMME is stated as being rank-normalised with 0.5 as a threshold for damaging variants. On checking the data downloaded from the site, GEMME was not rank-normalised but rather min-max normalised. Furthermore, Supplementary text S4 conflicts with the methods section over how GEMME scores are classified, S4 states that a raw-value threshold of -3 is used.
• Note. This is a major comment as one of the claims is that the associated web-tool is user-friendly. While functional, the web app is very awkward to use for analysis on any more than a few variants at once.
  • The fixed window size of the protein table necessitates excessive scrolling to reach your protein-of-interest. This will also get worse as more proteins are added. Suggestion: add a search/filter bar.
  • The same applies to the dataset window.
  • You are unable to copy anything out of the tables.
  • Hyperlinks in the tables only seem to work if you open them in a new tab or window.
  • All entries in the reference column point to the MAVISp preprint even when data from other sources is displayed (e.g. MAVE studies).
  • Entering multiple mutants in the "mutations to be displayed" window is time-consuming for more than a handful of mutants. Suggestion: Add a box where multiple mutants can be pasted in at once from an external document.

Minor comments

• Grammar. I appreciate that this manuscript may have been compiled by a non-native English speaker, but I would be remiss not to point out that there are numerous grammar errors throughout, usually sentence order issues or non-pluralisation. The meaning of the authors is mostly clear, but I recommend very thoroughly proof-reading the final version.
• There are numerous proteins that I know have high-quality MAVE datasets that are absent in the database e.g. BRCA1, HRAS and PPARG.
• Checking one of the existing MAVE datasets (KRAS), I found that the variants were annotated as damaging, neutral or given a positive score (these appear to stand-in for gain-of-function variants). For better correspondence with the other columns, those with positive scores could be labelled as 'ambiguous' or 'uncertain'.
• Numerous thresholds are defined for stabilizing / destabilizing / neutral variants in both the STABILITY and the LOCAL_INTERACTION modules. How were these thresholds determined? I note that (PMC9795540) uses a ΔΔG threshold of 1/-1 for defining stabilizing and destabilizing variants, which is relatively standard (though they also say that 2-3 would likely be better for pinpointing pathogenic variants).
• "Overall, with the examples in this section, we illustrate different applications of the MAVISp results, spanning from benchmarking purposes, using the experimental data to link predicted functional effects with structural mechanisms or using experimental data to validate the predictions from the MAVISp modules."

The last of these points is not an application of MAVISp, but rather a way in which external data can help validate MAVISp results. Furthermore, none of the examples given demonstrate an application in benchmarking (what is being benchmarked?). - Transcription factors section. This section describes an intended future expansion to MAVISp, not a current feature, and presents no results. As such, it should probably be moved to the conclusions/future directions section. - Figures. The dot-plots generated by the web app, and in Figures 4, 5 and 6 have 2 legends. After looking at a few, it is clear that the lower legend refers to the colour of the variant on the X-axis - most likely referencing the ClinVar effect category. This is not, however, made clear either on the figures or in the app. - "We identified ten variants reported in ClinVar as VUS (E102K, H86D, T29I, V91I, P2R, L44P, L44F, D56G, R11L, and E25Q, Fig.5a)"

E25Q is benign in ClinVar and has had that status since first submitted.

Significance

Platforms that aggregate predictors of variant effect are not a new concept, for example dbNSFP is a database of SNV predictions from variant effect predictors and conservation predictors over the whole human proteome. Predictors such as CADD and PolyPhen-2 will often provide a summary of other predictions (their features) when using their platforms. MAVISp's unique angle on the problem is in the inclusion of diverse predictors from each of its different moules, giving a much wider perspective on variants and potentially allowing the user to identify the mechanistic cause of pathogenicity. The visualisation aspect of the web app is also a useful addition, although the user interface is somewhat awkward. Potentially the most valuable aspect of this study is the associated gitbook resource containing reports from biocurators for proteins that link relevant literature and analyse ClinVar variants. Unfortunately, these are only currently available for a small minority of the total proteins in the database with such reports.

For improvement, I think that the paper should focus more on the precise utility of the web app / gitbook reports and how to interpret the results rather than going into detail about the underlying pipeline.

In terms of audience, the fast look-up and visualisation aspects of the web-platform are likely to be of interest to clinicians in the interpretation of variants of unknown clinical significance. The ability to download the fully processed dataset on a per-protein database would be of more interest to researchers focusing on specific proteins or those taking a broader view over multiple proteins (although a facility to download the whole database would be more useful for this final group).

My expertise.

• I am a protein bioinformatician with a background in variant effect prediction and large-scale data analysis.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

This study explores chromatin organization around trans-splicing acceptor sites (TASs) in the trypanosomatid parasites Trypanosoma cruzi, T. brucei and Leishmania major. By systematically re-analyzing MNase-seq and MNase-ChIP-seq datasets, the authors conclude that TASs are protected by an MNase-sensitive complex that is, at least in part, histone-based, and that single-copy and multi-copy genes display differential chromatin accessibility. Altogether, the data suggest a common chromatin landscape at TASs and imply that chromatin may modulate transcript maturation, adding a new regulatory layer to an unusual gene-expression system.

I value integrative studies of this kind and appreciate the careful, consistent data analysis the authors implemented to extract novel insights. That said, several aspects require clarification or revision before the conclusions can be robustly supported. My main concerns are listed below, organized by topic/result section.

TAS prediction * Why were TAS predictions derived only from insect-stage RNA-seq data? Restricting TAS calls to one life stage risks biasing predictions toward transcripts that are highly expressed in that stage and may reduce annotation accuracy for lowly expressed or stage-specific genes. Please justify this choice and, if possible, evaluate TAS robustness using additional transcriptomes or explicitly state the limitation.

TAS predictions derived only from insect-stage RNA-seq data because in a previous study it was shown that there are no significant differences between stages in the 5’UTR procesing in T. cruzi life stages (https://doi.org/10.3389/fgene.2020.00166) We are not testing an additional transcriptome here, because the robustness of the software was already probed in the original article were UTRme was described (Radio S, 2018 doi:10.3389/fgene.2018.00671).

Results - "There is a distinctive average nucleosome arrangement at the TASs in TriTryps": * You state that "In the case of L. major the samples are less digested." However, Supplementary Fig. S1 suggests that replicate 1 of L. major is less digested than the T. brucei samples, while replicate 2 of L. major looks similarly digested. Please clarify which replicates you reference and correct the statement if needed.

The reviewer has a good point. We made our statement based on the value of the maximum peak of the sequenced DNA molecules, which in general is a good indicative of the extension of the digestion achieved by the sample (Cole H, NAR, 2011).

As the reviewer correctly points, we should have also considered the length of the DNA molecules in each percentile. However, in this case both, T. brucei’s and L major’s samples were gel purified before sequencing and it is hard to know exactly what fragments were left behind in each case. Therefore, it is better not to over conclude on that regard.

We have now comment on this in the main manuscript, and we have clarified in the figure legends which data set we used in each case.

* It appears you plot one replicate in Fig. 1b and the other in Suppl. Fig. S2. Please indicate explicitly which replicate is in each plot. For T. brucei, the NDR upstream of the TAS is clearer in Suppl. Fig. S2 while the TAS protection is less prominent; based on your digestion argument, this should correspond to the more-digested replicate. Please confirm.

The replicates used for the construction of each figure are explicitly indicated in Table S1. Although we have detailed in the table the original publication, the project and accession number for each data set, the reviewer is correct that in this case it was still not completely clear to which length distribution heatmap was each sample associated with. To avoid this confusion, we have now added the accession number for each data set to the figure legends and also clarified in Table S1. Regarding the reviewer’s comment on the correspondence between the observed TAS protection and the extent of samples digestion, he/she is correct that for a more digested sample we would expect a clearer NDR. In this case, the difference in the extent of digestion between these two samples is minor, as observed the length of the main peak in the length distribution histogram for sequenced DNA molecules is the same. These two samples GSM5363006, represented in Fig1 b, and GSM5363007, represented in S2, belong to the same original paper (Maree et al 2017), and both were gel purified before sequencing. Therefore, any difference between them could not only be the result of a minor difference in the digestion level achieved in each experiment but could be also biased by the fragments included or not during gel purification. Therefore, I would not over conclude about TAS protection from this comparison. We have now included a brief comment on this, in the figure discussion

* The protected region around the TAS appears centered on the TAS in T. brucei but upstream in L. major. This is an interesting difference. If it is technical (different digestion or TAS prediction offset), explain why; if likely biological, discuss possible mechanisms and implications.

We appreciate the reviewer suggestion. We cannot assure if it is due to technical or biological reasons, but there is evidence that L. major ‘s genome has a different dinucleotide content and it might have an impact on nucleosome assembly. We have now added a comment about this observation in the final discussion of the manuscript.

Results - "An MNase sensitive complex occupies the TASs in T. brucei": * The definition of "MNase activity" and the ordering of samples into Low/Intermediate/High digestion are unclear. Did you infer digestion levels from fragment distributions rather than from controlled experimental timepoints? In Suppl. Fig. S3a it is not obvious how "Low digestion" was defined; that sample's fragment distribution appears intermediate. Please provide objective metrics (e.g., median fragment length, fraction 120-180 bp) used to classify digestion levels.

As the reviewer suggests, the ideal experiment would be to perform a time course of MNase reaction with all the samples in parallel, or to work with a fixed time point adding increasing amounts of MNase. However, even when making controlled experimental timepoints, you need to check the length distribution histogram of sequenced DNA molecules to be sure which level of digestion you have achieved.

In this particular case, we used public available data sets to make this analysis. We made an arbitrary definition of low, intermediate and high level of digestion, not as an absolute level of digestion, but as a comparative output among the tested samples. We based our definition on the comparison of __the main peak in length distribution heatmaps because this parameter is the best metric to estimate the level of digestion of a given sample. It represents the percentage of the total DNA sequenced that contains the predominant length in the sample tested. __Hence, we considered:

low digestion: when the main peak is longer than the expected protection for a nucleosome (longer than 150 bp). We expect this sample to contain additional longer bands that correspond to less digested material.

intermediate digestion, when the main peak is the expected for the nucleosome core-protection (˜146-150bp).

high digestion, when the main peak is shorter than that (shorter than 146 bp). This case, is normally accompanied by a bigger dispersion in fragment sizes.

To do this analysis, we chose samples that render different MNase protection of the TAS when plotting all the sequenced DNA molecules relative to this point and we used this protection as a predictor of the extent of sample digestion (Figure 2). To corroborate our hypothesis, that the degree of TAS protection was indeed related to the extent of the MNase digestion of a given sample, we looked at the length distribution histogram of the sequenced DNA molecules in each case. It is the best measurement of the extent of the digestion achieved, especially, when sequencing the whole sample without any gel purification and representing all the reads in the analysis as we did. The only caveat is with the sample called “intermediate digestion 1” that belongs to the original work of Mareé 2017, since only this data set was gel purified.

Whether the sample used in Figure 1 (from Mareé 2017) is also from the same lab and is an MNase-seq. Strictly speaking, there is no methodological difference between MNase-seq and the input of a native MNase-ChIP-seq, since the input does not undergo the IP.

* Several fragment distributions show a sharp cutoff at ~100-125 bp. Was this due to gel purification or bioinformatic filtering? State this clearly in Methods. If gel purification occurred, that can explain why some datasets preserve the MNase-sensitive region.

The sharp cutoff is neither due to gel purification or bioinformatic filtering, it is just due to the length of the paired-end read used in each case. In earlier works the most common was to sequence only 50bp, with the improvement of technologies it went up to 75,100 or 125 bp. We have now clarified in Table S1 the length of the paired-reads used in each case when possible.

* Please reconcile cases where samples labeled as more-digested contain a larger proportion of >200 bp fragments than supposedly less-digested samples; this ordering affects the inference that digestion level determines the loss/preservation of TAS protection. Based on the distributions I see, "Intermediate digestion 1" appears most consistent with an expected MNase curve - please confirm and correct the manuscript accordingly.

As explained above, it's a common observation in MNase digestion of chromatin that more extensive digestion can still result in a broad range of fragment sizes, including some longer fragments. This seemingly counter-intuitive result is primarily due to the non-uniform accessibility of chromatin and the sequence preference of the MNase enzyme, which has a preference for AT reach sequences.

The rationale of this is as follows: when you digest chromatin with MNase and the objective is to map nucleosomes genome-wide, the ideal situation would be to get the whole material contained in the mononucleosome band. Given that MNase is less efficient to digest protected DNA but, if the reaction proceeds further, it always ends up destroying part of it, the result is always far from perfect. The better situation we can get, is to obtain samples were ˜80% of the material is contained in the mononucloesome band. __And here comes the main point: __even in the best scenario, you always get some additional longer bands, such as those for di or tri nucleosomes. If you keep digesting, you will get less than 80 % in the nucleosome band and, those remaining DNA fragments that use to contain di and tri nucleosomes start getting digested as well, originating a bigger dispersion in fragments sizes. How do we explain persistence of Long Fragments? The longest fragments (di-, tri-nucleosomes) that persist in a highly digested sample are the ones that were originally most highly protected by proteins or higher-order structure, or by containing a poor AT sequence content, making their linker DNA extremely resistant to initial cleavage. Once the majority of the genome is fragmented, these few resistant longer fragments become a more visible component of the remaining population, contributing to a broader size dispersion. Hence, you end up observing a bigger dispersion in length distributions in the final material. Bottom line, it is not a good practice to work with under or over digested samples. Our main point, is to emphasize that especially when comparing samples, it important to compare those with comparable levels of digestion. Otherwise, a different sampling of the genome will be represented in the remaining sequenced DNA.

Results - "The MNase sensitive complexes protecting the TASs in T. brucei and T. cruzi are at least partly composed of histones": * The evidence that histones are part of the MNase-sensitive complex relies on H3 MNase-ChIP signal in subnucleosomal fragment bins. This seems to conflict with the observation (Fig. 1) that fragments protecting TASs are often nucleosome-sized. Please reconcile these points: are H3 signals confined to subnucleosomal fragments flanking the TAS while the TAS itself is depleted of H3? Provide plots that compare MNase-seq and H3 ChIP signals stratified by consistent fragment-size bins to clarify this.

What we learned from other eukaryotic organisms that were deeply studied, such as yeast, is that NDRs are normally generated at regulatory points in the genome. In this sense, yeast tRNA genes have a complex with a bootprint smaller than a nucleosome formed by TFIIIC-TFIIB (Nagarajavel, doi: 10.1093/nar/gkt611). On the other hand, many promotor regions have an MNase-sensitive complex with a nucleosome-size footprint, but it does not contain histones (Chereji, et al 2017, doi:10.1016/j.molcel.2016.12.009). The reviewer is right that from Figure 1 and S2 we could observe that the footprint of whatever occupies the TAS region, especially in T. brucei, is nucleosome-size. However, it only shows the size, but it doesn’t prove the nature of its components. Nevertheless, those are only MNase-seq data sets. Since it does not include a precipitation with specific antibodies, we cannot confirm the protecting complex is made up by histones. In parallel, a complementary study by Wedel 2017, from Siegel’s lab, shows that using a properly digested sample and further immunoprecipitating with a-H3 antibody, the TAS is not protected by nucleosomes at least not when analyzing nucleosome size-DNA molecules. Besides, Briggs et. al 2018 (doi: 10.1093/nar/gky928) showed that at least at intergenic regions H3 occupancy goes down while R-loops accumulation increases. We have now added a supplemental figure associated to Figure 3 (new Suplemental 5) replotting R-loops and MNase-ChIP-seq for H3 relative to our predicted TAS showing this anti-correlation and how it partly correlates with MNase protection as well. As a control we show that Rpb9 trends resembles H3 as Siegel’s lab have shown in Wedel 2018.

* Please indicate which datasets are used for each panel in Suppl. Fig. S4 (e.g., Wedel et al., Maree et al.), and avoid calling data from different labs "replicates" unless they are true replicates.

In most of our analysis we used real replicated experiments. Such is the case MNase-seq data used in Figure 1, with the corresponding replicate experiments used in Figure S2; T. cruzi MNase-ChIP-seq data used in Figure 3b and 4a with the respective replicate used in Figures S4 and S5 (now S6 in the revised manuscript). The only case in which we used experiments coming from two different laboratories, is in the case of MNase-ChIP-seq for H3 from T. brucei. Unfortunately, there are only two public data sets coming each of them from different laboratories. The samples used in Fig 3 (from Siegel’s lab) whether the IP from H3 represented in S4 and S5 (S6 n the updated version) comes from another lab (Patterton’s). To be more rigorous, we now call them data 1 and 2 when comparing these particular case.

The reviewer is right that in this particular case one is native chromatin (Pattertons’) while the other one is crosslinked (Siegel’s). We have now clarified it in the main text that unfortunately we do not count on a replicate but even under both condition the result remains the same, and this is compatible with my own experience, were crosslinking does not affect the global nucleosome patterns (compared nucleosome organization from crosslinked chromatin MNAse-seq inputs Chereji, Mol Cell, 2017 doi: 10.1016/j.molcel.2016.12.009 and native MNase-seq from Ocampo, NAR, 2016 doi: 10.1093/nar/gkw068).

* Several datasets show a sharp lower bound on fragment size in the subnucleosomal range (e.g., ~80-100 bp). Is this a filtering artifact or a gel-size selection? Clarify in Methods and, if this is an artifact, consider replotting after removing the cutoff.

We have only filtered adapter dimmer or overrepresented sequences when needed. In Figures 2 and S3 we represented all the sequenced reads. In other figures when we sort fragments sizes in silico, such as nucleosome range, dinucleosome or subnucleosome size, we make a note in the figure legends. What the reviewer points is related to the length of the sequence DNA fragment in each experiment. As we explained above, the older data-sets were performed with 50 bp paired-end reads, the newer ones are 75, 100 or 125bp. This is information is now clarified in Table S1.

__Results - "The TASs of single and multi-copy genes are differentially protected by nucleosomes": __

__ __* Please include T. brucei RNA-seq data in Suppl. Fig. S5b as you did for T. cruzi.

We have shown chromatin organization for T. brucei in S5b to show that there is a similar trend. Unfortunately, we did not get a robust list of multi-copy genes for T. brucei as we did get for T. cruzi, therefore we do not want to over conclude showing the RNA-seq for these subsets of genes. The limitation is related to the fact that UTRme restrict the search and is extremely strict when calling sites at repetitive regions.

* Discuss how low or absent expression of multigene families affects TAS annotation (which relies on RNA-seq) and whether annotation inaccuracies could bias the observed chromatin differences.

The mapping of occurrence and annotations that belong to repetitive regions has great complexity. UTRme is specially designed to avoid overcalling those sites. In other words, there is a chance that we could be underestimating the number of predicted TASs at multi-copy genes. Regarding the impact on chromatin analysis, we cannot rule out that it might have an impact, but the observation favors our conclusion, since even when some TASs at multi-copy genes can remain elusive, we observe more nucleosome density at those places.

* The statement that multi-copy genes show an "oscillation" between AT and GC dinucleotides is not clearly supported: the multi-copy average appears noisier and is based on fewer loci. Please tone down this claim or provide statistical support that the pattern is periodic rather than noisy.

We have fixed this now in the preliminary revised version

* How were multi-copy genes defined in T. brucei? Include the classification method in Methods.

This classification was done the same way it was explained for T. cruzi

Genomes and annotations: * If transcriptomic data for the Y strain was used for T. cruzi, please explain why a Y strain genome was not used (e.g., Wang et al. 2021 GCA_015033655.1), or justify the choice. For T. brucei, consider the more recent Lister 427 assembly (Tb427_2018) from TriTrypDB. Use strain-matched genomes and transcriptomes when possible, or discuss limitations.

The most appropriate way to analyze high throughput data, is to aline it to the same genome were the experiments were conducted. This was clearly illustrated in a previous publication from our group were we explained how should be analyzed data from the hybrid CL Brener strain. A common practice in the past was to use only Esmeraldo-like genome for simplicity, but this resulted in output artifacts. Therefore, we aligned it to CL Brener genome, and then focused the main analysis on the Esmeraldo haplotype (Beati Plos ONE, 2023). Ideally, we should have counted on transcriptomic data for the same strain (CL Brener or Esmeraldo). Since this was not the case at that moment, we used data from Y strain that belongs to the same DTU with Esmeraldo.

In the case of T. brucei, when we started our analysis and the software code for UTRme was written, the previous version of the genome was available. Upon 2018 version came up, we checked chromatin parameters and observed that it did not change the main observations. Therefore, we continue working with our previous setups.

Reproducibility and broader integration: * Please share the full analysis pipeline (ideally on GitHub/Zenodo) so the results are reproducible from raw reads to plots.

We are preparing a full pipeline in GitHub. We will make it available before manuscript full revision

* As an optional but helpful expansion, consider including additional datasets (other life stages, BSF MNase-seq, ATAC-seq, DRIP-seq) where available to strengthen comparative claims.

We are now including a new suplemental figure including DRIP-seq and Rp9 ChIP-seq (revised S5). Additionally, we added a new panel c to figure 4, representing FAIRE-seq data for T. cruzi fore single and multi-copy genes

We are working on ATAC-seq analysis and BSF MNase-seq

Optional analyses that would strengthen the study: * Stratify single-copy genes by expression (high / medium / low) and examine average nucleosome occupancy at TASs for each group; a correlation between expression and NDR depth would strengthen the functional link to maturation.

We have now included a panel in suplemental figure 5 (now revised S6), showing the concordance for chromatin organization of stratified genes by RNA-seq levels relative to TAS.

__Minor / editorial comments: __ * In the Introduction, the sentence "transcription is initiated from dispersed promoters and in general they coincide with divergent strand switch regions" should be qualified: such initiation sites also include single transcription start regions.

We have clarified this in the preliminary revised version

* Define the dotted line in length distribution plots (if it is not the median, please clarify) and consider placing it at 147 bp across plots to ease comparison.

The dotted line is just to indicate where the maximum peak is located. It is now clarified in figure legends.

* In Suppl. Fig. 4b "Replicate2" the x-axis ticks are misaligned with labels - please fix.

We have now fixed the figure. Thanks for noticing this mistake.

* Typo in the Introduction: "remodellingremodeling" → "remodeling

Thanks for noticing this mistake, it is fixed in the current version of the manuscript

**Referee cross-commenting** Comment 1: I think Reviewer #2 and Reviewer #3 missed that they authors of this manuscript do cite and consider the results from Wedel at al. 2017. They even re-analysed their data (e.g. Figure 3a). I second Reviewer #2 comment indicating that the inclusion of a schematic figure to help readers visualize and better understand the findings would be an important addition.

Comment 2: I agree with Reviewer #3 that the use of different MNase digestion procedures in the different datasets have to be considered. On the other hand, I don't think there is a problem with figure 1 showing an MNase-protected TAS for T. brucei as it is based on MNase-seq data and reproduces the reported results (Maree et al. 2017). What the Siegel lab did in Wedel et al. 2017 was MNase-ChIPseq of H3 showing nucleosome depletion at TAS, but both results are not necessary contradictory: There could still be something else (which does not contain H3) sitting on the TAS protecting it from MNase digestion.

Reviewer #1 (Significance (Required)):

This study provides a systematic comparative analysis of chromatin landscapes at trans-splicing acceptor sites (TASs) in trypanosomatids, an area that has been relatively underexplored. By re-analyzing and harmonizing existing MNase-seq and MNase-ChIP-seq datasets, the authors highlight conserved and divergent features of nucleosome occupancy around TASs and propose that chromatin contributes to the fidelity of transcript maturation. The significance lies in three aspects: 1. Conceptual advance: It broadens our understanding of gene regulation in organisms where transcription initiation is unusual and largely constitutive, suggesting that chromatin can still modulate post-transcriptional processes such as trans-splicing. 2. Integrative perspective: Bringing together data from T. cruzi, T. brucei and L. major provides a comparative framework that may inspire further mechanistic studies across kinetoplastids. 3. Hypothesis generation: The findings open testable avenues about the role of chromatin in coordinating transcript maturation, the contribution of DNA sequence composition, and potential interactions with R-loops or RNA-binding proteins. Researchers in parasitology, chromatin biology, and RNA processing will find it a useful resource and a stimulus for targeted experimental follow-up.

My expertise is in gene regulation in eukaryotic parasites, with a focus on bioinformatic analysis of high-throughput sequencing data

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

Siri et al. perform a comparative analysis using publicly available MNase-seq data from three trypanosomatids (T. brucei, T. cruzi, and Leishmania), showing that a similar chromatin profile is observed at TAS (trans-splicing acceptor site) regions. The original studies had already demonstrated that the nucleosome profile at TAS differs from the rest of the genome; however, this work fills an important gap in the literature by providing the most reliable cross-species comparison of nucleosome profiles among the tritryps. To achieve this, the authors applied the same computational analysis pipeline and carefully evaluated MNase digestion levels, which are known to influence nucleosome profiling outcomes.

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. The manuscript could be improved with some clarifications and adjustments:

1. The authors state from the beginning that available MNase data indicate altered nucleosome occupancy around the TAS. However, they could also emphasize that the conclusions across the different trypanosomatids are inconsistent and even contradictory: NDR in T. cruzi versus protection-in different locations-in T. brucei and Leishmania.

We start our manuscript by referring to the first MNase-seq data sets publicly available for each TriTryp and we point that one of the main observations, in each of them, is the occurrence of a change in nucleosome density or occupancy at intergenic regions. In T. cruzi, in a previous publication from our group, we stablished that this intergenic drop in nucleosome density occurs near the trans-splicing acceptor site. In this work, we extend our study to the other members of TriTryps: T. brucei and L. major.

In T. brucei the papers from Patterton’s lab and Siegel’s lab came out almost simultaneously in 2017. Hence, they do not comment on each other’s work. The first one claims the presence of a well-positioned nucleosome at the TAS by using MNase-seq, while the second one, shows an NDR at the TAS by using MNase-ChIP-seq. However, we do not think they are contradictory, or they have inconsistency. We brought them together along the manuscript because we think these works can provide complementary information.

On one hand, we infer data from Pattertons lab is slightly less digested than the sample from Siegel’s lab. Therefore, we discuss that this moderate digestion must be the reason why they managed to detect an MNase protecting complex sitting at the TAS (Figure 1). On the other hand, Sigel’s lab includes an additional step by performing MNase-ChIP-seq, showing that when analyzing nucleosome size fragments, histones are not detected at the TAS. Here, we go further in this analysis on figure 3, showing that only when looking at subnucleosome-size fragments, we are able to detect histone H3. And this is also true for T. cruzi.

By integrating every analysis in this work and the previous ones, we propose that TASs are protected by an MNase-sensitive complex (probed in Figure 2). This complex most likely is only partly formed by histones, since only when analyzing sub-nucleosomes size DNA molecules we can detect histone H3 (Figure 3). To be absolutely sure that the complex is not entirely made up by histones, future studies should perform an MNse-ChIP-seq with less digested samples. However, it was previously shown that R-loops are enriched at those intergenic NDRs (Briggs, 2018 doi: 10.1093/nar/gky928) and that R-loops have plenty of interacting proteins (Girasol, 2023 10.1093/nar/gkad836). Therefore, most likely, this MNase-sensitive complexed have a hybrid nature made up by H3 and some other regulatory molecules, possibly involved in trans-splicing. We have now added a new figure S5 showing R-loop co-localization with the NDR.

Regarding the comparison between different organisms, after explaining the sensitivity to MNase of the TAS protecting complex, we discuss that when comparing equally digested samples T. cruzi and T. brucei display a similar chromatin landscape with a mild NDR at the TAS (See T. cruzi represented in Figure 1 compared to T. brucei represented in Intermediate digestion 2 in Figure 2, intermediate digestion in the revised manuscript). Unfortunately, we cannot make a good comparison with L. major, since we do not count on a similar level of digestion.

Another point that requires clarification concerns what the authors mean in the introduction and discussion when they write that trypanosomes have "...poorly organized chromatin with nucleosomes that are not strikingly positioned or phased." On the other hand, they also cite evidence of organization: "...well-positioned nucleosome at the spliced-out region.. in Leishmania (ref 34)"; "...a well-positioned nucleosome at the TASs for internal genes (ref37)"; "...a nucleosome depletion was observed upstream of every gene (ref 35)." Aren't these examples of organized chromatin with at least a few phased nucleosomes? In addition, in ref 37, figure 4 shows at least two (possibly three to four) nucleosomes that appear phased. In my opinion, the authors should first define more precisely what they mean by "poorly organized chromatin" and clarify that this interpretation does not contradict the findings highlighted in the cited literature.

For a better understanding of nucleosome positioning and phasing I recommend the review: Clark 2010 doi:10.1080/073911010010524945, Figure 4. Briefly, in a cell population there are different alternative positions that a given nucleosome can adopt. However, some are more favorable. When talking about favorable positions, we refer to the coordinates in the genome that are most likely covered by a nucleosome and are predominant in the cell population. Additionally, nucleosomes could be phased or not. This refers not only the position in the genome, but to the distance relative to a given point. In yeast, or in highly transcribed genes of more complex eukaryotes, nucleosomes are regularly spaced and phased relative to the transcription start site (TSS) or to the +1 nucleosome (Ocampo, NAR, 2016, doi:10.1093/nar/gkw068). In trypanosomes, nucleosomes have some regular distribution when making a browser inspection but, given that they are not properly phased with respect to any point, it is almost impossible to make a spacing estimation from paired-end data. This is also consistent with a chromatin that is transcribed in an almost constitutive manner.

As the reviewer mention, we do site evidence of organization. We think the original observations are correct, but we do not fully agree with some of the original statements. In this manuscript our aim is to take the best we learned from their original works and to make a constructive contribution adding to the original discussions. In this regard, in trypanosomes there are some conserved patterns in the chromatin landscape, but their nucleosomes are far from being well-positioned or phased. For a better understanding, compare the variations observed in the y axis when representing av. nucleosome occupancy in yeast with those observed in trypanosomes and you will see that the troughs and peaks are much more prominent in yeast than the ones observed in any TryTryp member.

Following the reviewer’s suggestion we have now clarified this in the main text

The paper would also benefit from the inclusion of a schematic figure to help readers visualize and better understand the findings. What is the biological impact of having nucleosomes, di-nucleosomes, or sub-nucleosomes at TAS? This is not obvious to readers outside the chromatin field. For example, the following statement is not intuitive: "We observed that, when analyzing nucleosome-size (120-180 bp) DNA molecules or longer fragments (180-300 bp), the TASs of either T. cruzi or T. brucei are mostly nucleosome-depleted. However, when representing fragments smaller than a nucleosome-size (50-120 bp) some histone protection is unmasked (Fig. 3 and Fig. S4). This observation suggests that the MNase sensitive complex sitting at the TASs is at least partly composed of histones." Please clarify.

We appreciate the reviewer’s suggestion to make a schematic figure. We are working on this and will be added to the manuscript upon final revision.

Regarding the biological impact of having mono, di or subnucleosome fragments, it is important to unveil the fragment size of the protected DNA to infer the nature of the protecting complex. In the case of tRNA genes in yeast, at pol III promoters they found footprints smaller than a nucleosome size that ended up being TFIIB-TFIIC (Nagarajavel, doi: 10.1093/nar/gkt611). Therefore, detecting something smaller than a nucleosome might suggest the binding of trans-acting factors different than histones or involving histones in a mixed complex. These mixed complexes are also observed, and that is the case of the centromeric nucleosome which has a very peculiar composition (Ocampo and Clark, Cells Reports, 2015). On the other hand, if instead we detect bigger fragments, it could be indicative of the presence of bigger protecting molecules or that those regions are part of higher order chromatin organization still inaccessible for MNase linker digestions.

Here we show on 2Dplots, that complex or components protecting the TAS have nucleosome size, but we cannot assure they are entirely made up by histones, since, only when looking at subnucleosome-size fragments, we are able to detect histone H3. We have now added part of this explanation to the discussion.

By integrating every analysis in this work and the previous ones, we propose that the TAS is protected by an MNase-sensitive complex (Figure 2). This complex most likely is only partly formed by histones, since only when analyzing sub-nucleosomes size DNA molecules we can detect histone H3 (Figure 3). As explained above, to be absolutely sure that the complex is not entirely made up by histones, future studies should perform an MNse-ChIP-seq with less digested samples. However, it was previously shown that R-loops are enriched at those intergenic NDRs (Briggs 2018) and that R-loops have plenty of interacting proteins (Girasol, 2023). Therefore, most likely, this MNase-sensitive complexed have a hybrid nature made up by H3 and some other regulatory molecules. We have now added a new S5 figure showing R-loop co-localization.

Some references are missing or incorrect:

we will make a thorough revision

"In trypanosomes, there are no canonical promoter regions." - please check Cordon-Obras et al. (Navarro's group). Thank you for the appropiate suggestion.

We have now added this reference

Please, cite the study by Wedel et al. (Siegel's group), which also performed MNase-seq analysis in T. brucei.

We understand that reviewer number 2# missed that we cited this reference and that we did used the raw data from the manuscript of Wedel et. al 2017 form Siegel’s group. We used the MNase-ChIP-seq data set of histone H3 in our analysis for Figures 3, S4b and S5b (S6c in the revised version), also detailed in table S1. To be even more explicit we have now included the accession number of each data set in the figure legend.

Figure-specific comments: Fig. S3: Why does the number of larger fragments increase with greater MNase digestion? Shouldn't the opposite be expected?

This a good observation. As we also explained to reviewer#1:

It's a common observation in MNase digestion of chromatin that more extensive digestion can still result in a broad range of fragment sizes, including some longer fragments. This seemingly counter-intuitive result is primarily due to the non-uniform accessibility of chromatin and the sequence preference of the MNase enzyme.

The rationale of this is as follows: when you digest chromatin with MNase and the objective is to map nucleosomes genome-wide, the ideal situation would to get the whole material contained in the mononucleosome band. Given that MNase is less efficient to digest protected DNA but, if the reaction proceeds further, it always ends up destroying part of it, the result is always far from perfect. The better situation we can get, is to obtain samples were ˜80% of the material is contained in the mononucloesome band. __And here comes the main point: __even in the best scenario, you always have some additional longer bands, such as those for di or tri nucleosomes. If you keep digesting, you will get less than 80 % in the nucleosome band and, those remaining DNA fragments that use to contain di and tri nucleosomes start getting digested as well originating a bigger dispersion in fragments sizes. How do we explain persistence of Long Fragments? The longest fragments (di-, tri-nucleosomes) that persist in a highly digested sample are the ones that were originally most highly protected by proteins or higher-order structure, making their linker DNA extremely resistant to initial cleavage. Once the majority of the genome is fragmented, these few resistant longer fragments become a more visible component of the remaining population, contributing to a broader size dispersion. Hence, there you end up having a bigger dispersion in length distributions in the final material. Bottom line, it is not a good practice to work with under or overdigested samples. Our main point is to emphasize that especially when comparing samples, it important to compare those with comparable levels of digestion. Otherwise, a different sampling of the genome will be represented in the remaining sequenced DNA Fig. S5B: Why not use MNase conditions under which T. cruzi and T. brucei display comparable profiles at TAS? This would facilitate interpretation.

The reviewer made a reasonable observation. The reason why we used MNase-ChIP_seq instead of just MNase to test occupancy at TAS at the subsets of genes, is because we intended to be more certain if we were talking about the presence of histones or something else. By using IP for histone H3 we can see that at multi-copy genes this protein is present when looking at nucleosome-size fragments. Additionally, as shown in figure S4b, length distribution histograms are also similar for the compared IPs.

Minor points:

There are several typos throughout the manuscript.

Thanks for the observation. We will check carefully.

Methods: "Dinucelotide frecuency calculation."

We will add a code in GitHub

Reviewer #2 (Significance (Required)):

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. Audience: basic science and specialized readers.

Expertise: epigenetics and gene expression in trypanosomatids.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __

The authors analysed publicly accessible MNase-seq data in TriTryps parasites, focusing on the chromatin structure around trans-splicing acceptor sites (TASs), which are vital for processing gene transcripts. They describe a mild nucleosome depletion at the TAS of T. cruzi and L. major, whereas a histone-containing complex protects the TASs of T. brucei. In the subsequent analysis of T. brucei, they suggest that a Mnase-sensitive complex is localised at the TASs. For single-copy versus multi-copy genes, the authors show different di-nucleotide patterns and chromatin structures. Accordingly, they propose this difference could be a novel mechanism to ensure the accuracy of trans-splicing in these parasites.

Before providing an in- depth review of the manuscript, I note that some missing information would have helped in assessing the study more thoroughly; however, in the light of the available information, I provide the following comments for consideration.

The numbering of the figures, including the figure legends, is missing in the PDF file. This is essential for assessing the provided information.

We apologized for not including the figure numbers in the main text, although they are located in the right place when called in the text. The omission was unwillingly made when figure legends were moved to the bottom of the main text. This is now fixed in the updated version of the manuscript.

The publicly available Mnase- seq data are manyfold, with multiple datasets available for T. cruzi, for example. It is unclear from the manuscript which dataset was used for which figure. This must be clarified.

This was detailed in Table S1. We have now replaced the table by an improved version, and we have also included the accession number of each data set used in the figure legends.

Why do the authors start in figure 1 with the description of an MNase- protected TAS for T.brucei, given that it has been clearly shown by the Siegel lab that there is a nucleosome depletion similar to other parasites?

We did not want to ignore the paper from Patterton’s lab because it was the first one to map nucleosomes genome-wide in T. brucei and the main finding of that paper claimed the existence of a well-positioned nucleosome at intergenic regions, what we though constitutes a point worth to be discussed. While Patterton’s work use MNase-seq from gel-purified samples and provides replicated experiments sequenced in really good depth; Siegel’s lab uses MNase-ChIP-seq of histone H3 but performs only one experiment and its input was not sequenced. So, each work has its own caveats and provides different information that together contributes to make a more comprehensive study. We think that bringing up both data sets to the discussion, as we have done in Figures 1 and 3, helps us and the community working in the field to enrich the discussion.

If the authors re- analyse the data, they should compare their pipeline to those used in the other studies, highlighting differences and potential improvements.

We are working on this point. We will provide a more detail description in the final revision.

Since many figures resemble those in already published studies, there seems little reason to repeat and compare without a detailed comparison of the pipelines and their differences.

Following the reviewer advice, we are now working on highlighting the main differences that justify analyzing the data the way we did and will be added in the finally revised method section.

At a first glance, some of the figures might look similar when looking at the original manuscripts comparing with ours. However, with a careful and detailed reading of our manuscripts you can notice that we have added several analyses that allow to unveil information that was not disclosed before.

First, we perform a systematic comparison analyzing every data set the same way from beginning to end, being the main difference with previous studies the thorough and precise prediction of TAS for the three organisms. Second, we represent the average chromatin organization relative to those predicted TASs for TriTryps and discuss their global patterns. Third, by representing the average chromatin into heatmaps, we show for the very first time, that those average nucleosome landscape are not just an average, they keep a similar organization in most of the genome. These was not done in any of the previous manuscripts except for our own (Beati, PLOS One 2023). Additionally, we introduce the discussion of how the extension of MNase reaction can affect the output of these experiments and we show 2D-plots and length distribution heatmaps to discuss this point (a point completely ignored in all the chromatin literature for trypanosomes). Furthermore, we made a far-reaching analysis by considering the contributions of each publish work even when addressed by different techniques. Finally, we discuss our findings in the context of a topic of current interest in the field, such as TriTryp’s genome compartmentalization.

Several previous Mnase- seq analysis studies addressing chromatin accessibility emphasized the importance of using varying degrees of chromatin digestion, from low to high digestion (30496478, 38959309, 27151365).

The reviewer is correct, and this point is exactly what we intended to illustrate in figure number 2. We appreciate he/she suggests these references that we are now citing in the final discussion. Just to clarify, using varying degrees of chromatin digestion is useful to make conclusions about a given organism but when comparing samples, strains, histone marks, etc. It is extremely important to do it upon selection of similar digested samples.

No information on the extent of DNA hydrolysis is provided in the original Mnase- seq studies. This key information can not be inferred from the length distribution of the sequenced reads.

The reviewer is correct that “No information on the extent of DNA hydrolysis is provided in the original Mnase-seq studies” and this is another reason why our analysis is so important to be published and discussed by the scientific community working in trypanosomes. We disagree with the reviewer in the second statement, since the level of digestion of a sequenced sample is actually tested by representing the length distribution of the total DNA sequenced. It is true that before sequencing you can, and should, check the level of digestion of the purified samples in an agarose gel and/or in a bioanalyzer. It could be also tested after library preparation, but before sequencing, expecting to observe the samples sizes incremented in size by the addition of the library adapters. But, the final test of success when working with MNase digested samples is to analyze length of DNA molecules by representing the histograms with length distribution of the sequenced DNA molecules. Remarkably, on occasions different samples might look very similar when run in a gel, but they render different length distribution histograms and this is because the nucleosome core could be intact but they might have suffered a differential trimming of the linker DNA associated to it or even be chewed inside (see Cole Hope 2011, section 5.2, doi: 10.1016/B978-0-12-391938-0.00006-9, for a detailed explanation).

As the input material are selected, in part gel- purified mono- nucleosomal DNA bands. Furthermore the datasets are not directly comparable, as some use native MNase, while others employ MNase after crosslinking; some involve short digestion times at 37 {degree sign} C, while others involve longer digestion at lower temperatures. Combining these datasets to support the idea of an MNase- sensitive complex at the TAS of T. brucei therefore may not be appropriate, and additional experiments using consistent methodologies would strengthen the study's conclusions.

In my opinion, describing an MNase- sensitive complex based solely on these data is not feasible. It requires specifically designed experiments using a consistent method and well- defined MNase digestion kinetics.

As the reviewer suggests, the ideal experiment would be to perform a time course of MNase reaction with all the samples in parallel, or to work with a fix time point adding increasing amounts of MNase. However, the information obtained from the detail analysis of the length distribution histogram of sequenced DNA molecules the best test of the real outcome. In fact, those samples with different digestion levels were probably not generated on purpose.

The only data sets that were gel purified are those from Mareé 2017 (Patterton’s lab), used in Figures 1, S1 and S2 and those from L. major shown in Fig 1. It was a common practice during those years, then we learned that is not necessary to gel purify, since we can sort fragment sizes later in silico when needed.

As we explained to reviewer #1, to avoid this conflict, we decided to remove this data from figures 2 and S3. In summary, the 3 remaining samples comes from the same lab, and belong to the same publication (Mareé 2022). These sample are the inputs of native MNase ChIp-seq, obtain the same way, totally comparable among each other.

Reviewer #3 (Significance (Required)):

Due to the lack of controlled MNase digestion, use of heterogeneous datasets, and absence of benchmarking against previous studies, the conclusions regarding MNase-sensitive complexes and their functional significance remain speculative. With standardized MNase digestion and clearly annotated datasets, this study could provide a valuable contribution to understanding chromatin regulation in TriTryps parasites.

As we have explained in the previous point our conclusions are valid since we do not compare in any figure samples coming from different treatments. The only exception to this comment could be in figure 3 when talking about MNase-ChIP-seq. We have now added a clear and explicit comment in the section and the discussion that despite having subtle differences in experimental procedures we arrive to the same results. This is the case for T. cruzi IP, run from crosslinked chromatin, compared to T. brucei’s IP, run from native chromatin.

Along the years it was observed in the chromatin field that nucleosomes are so tightly bound to DNA that crosslinking is not necessary. However, it is still a common practice specially when performing IPs. In our own hands, we did not observe any difference at the global level neither in T. cruzi or in my previous work with yeast.

...

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this manuscript, the authors describe a good-quality ancient maize genome from 15th-century Bolivia and try to link the genome characteristics to Inca influence. Overall, the manuscript is below the standard in the field. In particular, the geographic origin of the sample and its archaeological context is not well evidenced. While dating of the sample and the authentication of ancient DNA have been evidenced robustly, the downstream genetic analyses do not support the conclusion that genomic changes can be attributed to Inca influence. Furthermore, sections of the manuscript are written incoherently and with logical mistakes. In its current form, this paper is not robust and possibly of very narrow interest. 

Strengths: 

Technical data related to the maize sample are robust. Radiocarbon dating strongly evidenced the sample age, estimated to be around 1474 AD. Authentication of ancient DNA has been done robustly. Spontaneous C-to-T substitutions, which are present in all ancient DNA, are visible in the reported sample with the expected pattern. Despite a low fraction of C-to-T at the 1st base, this number could be consistent with the cool and dry climate in which the sample was preserved. The distribution of DNA fragment sizes is consistent with expectations for a sample of this age. 

Weaknesses: 

Thank you for all your thoughtful comments. See below for comments on each.

(1) Archaeological context for the maize sample is weakly supported by speculation about the origin and has unreasonable claims weighing on it. Perhaps those findings would be more convincing if the authors were to present evidence that supports their conclusions: i) a map of all known tombs near La Paz, ii) evidence supporting the stone tomb origins of this assemblage, and iii) evidence supporting non-Inca provenance of the tomb. 

We believe we are clear about what information we have about context.  First, the intake records from the MSU Museum from 1890 are not as detailed as we would like, but we cannot enhance them. The mummified girl and her accoutrements, including the maize, came from a stone tower or chullpa south of La Paz, in what is now Bolivia. We do not know which stone chullpa, so a map would be of limited use.  The mortuary group is identified as Inca, but as we note the accoutrements do not appear of high status, so it is possible that she is not an elite.  Mud tombs are normally attributed to the local population, and stone towers to Inca or elites. We have clarified at multiple places in the text that the maize is from the period of Inca incursion in this part of Bolivia and have modified text to reflect greater uncertainty of Inca or local origin, but that selection for environmentally favorable characteristics had taken place.  Regardless, there are three 15th c CE or AD AMS ages on the maize, a cucurbita rind, and a camelid fiber.  The maize is almost certainly mid to late 15th century CE.

(2) Dismissal of the admixture in the reported samples is not evidenced correctly. Population f3 statistic with an outgroup is indeed one of the most robust metrics for sample relatedness; however, it should not be used as a test of admixture. For an admixture test, the population f3 statistic should be used in the form: i) target population, ii) one possible parental population, iii) another possible parental population. This is typically done iteratively with all combinations of possible parental populations. Even in such a form, the population f3 statistic is not very sensitive to admixture in cases of strong genetic drift, and instead population f4 statistic (with an outgroup) is a recommended test for admixture. 

We have removed “Our admixture f3-statistics test results suggest aBM is not admixed” in our revised manuscript. Since our goal here is to identify which group(s) has(have) the highest relatedness with aBM, so population f3 statistic with an outgroup is the most robust metric to do the test and to support our conclusion here.

(3) The geographic placement of the sample based on genetic data is not robust. To make use of the method correctly, it would be necessary to validate that genetic samples in this region follow the assumption of the 'isolation-by-distance' with dense sampling, which has not been done. Additionally, the authors posit that "This suggests that aBM might not only be genetically related to the archaeological maize from ancient Peru, but also in the possible geographic location." The method used to infer the location is based on pure genetic estimation. The above conclusion is not supported by this method, and it directly contradicts the authors' suggestion that the sample comes from Bolivia.  

We understood that it is necessary to validate the assumption of the 'isolation-by-distance' with dense sampling. But we did not do it because: 1) the ancient maize age ranges from ~5000BP to ~100BP and they were found in very different countries at different times. 2) isolation-by-distance is a population genetic concept and it's often used to test whether populations that are geographically farther apart are also more genetically different. Considering we only have 17 ancient samples in total our sample size is not sufficient for a big population test.

For "It directly contradicts the authors' suggestion that the sample comes from Bolivia.”, as we described in our manuscript that “Given the provenience of the aBM and its age, it is possible the samples were local or alternatively were introduced into western highland Bolivia from the Inca core area – modern Peru.” The sample recording file did show the aBM sample was found in Bolivia, but we do not know where aBM originally came from before it was found in Bolivia. To answer this question, we used locator.py to predict the potential geographic location that aBM may have originally come from, and our results showed that the predicted location is inside of modern Peru and is also very close to archaeological Peruvian maize.  

Therefore, our conclusion that "This suggests that aBM might not only be genetically related to the archaeological maize from ancient Peru, but also in the possible geographic location” does not contradict that the sample was found Bolivia.

(4) The conclusion that Ancient Andean maize is genetically similar to European varieties and hence shares a similar evolutionary history is not well supported. The PCA plot in Figure 4 merely represents sample similarity based on two components (jointly responsible for about 20% of the variation explained), and European samples could be very distant based on other components. Indeed, the direct test using the outgroup f3 statistic does not support that European varieties are particularly closely related to ancient Andean maize. Perhaps these are more closely related to Brazil? We do not know, as this has not been measured. 

Our conclusion is “We also found that a few types of maize from Europe have a much closer distance to the archaeological maize cluster compared to other modern maize, which indicates maize from Europe might expectedly share certain traits or evolutionary characteristics with ancient maize. It is also consistent with the historical fact that maize spread to Europe after Christopher Columbus's late 15th century voyages to the Americas. But as shown, maize also has diversity inside the European maize cluster. It is possible that European farmers and merchants may have favored different phenotypic traits, and the subsequent spread of specific varieties followed the new global geopolitical maps of the Colonial era”.

We understood your concerns that two components only explain about 20% of the variation. But as you can see from the Figure 2b in Grzybowski, M.W. et al., 2023 publication, it described that “the first principal component (PC1) of variation for genetic marker data roughly corresponded to the division between domesticated maize and maize wild relatives is only 1.3%”. It shows this is quite common in maize, especially when the datasets include landraces, hybrids, and wild relatives. For our maize dataset, we have archaeological maize data ranging from ~5,000BP to ~100BP, and we also have modern maize, which makes the genetic structure of our data more complicated. Therefore, we think our two components are currently the best explanation currently possible. We also included PCA plot based on component 1 and 3 in Fig4_PCA13.pdf. It does not show that the European samples are very distant.

For “Perhaps these are more closely related to Brazil?”, thank you for this very good question, but we apologize that we cannot answer this question from our current study because our study focuses on identifying the location where aBM originally came from, establishing and explaining patterns of genetic variability of maize, with a specific focus on maize strains that are related to our current aBM. Thus, we will not explore the story between maize from Brazil and European maize in our current study.

(5) The conclusion that long branches in the phylogenetic tree are due to selection under local adaptation has no evidence. Long branches could be the result of missing data, nucleotide misincorporations, genetic drift, or simply due to the inability of phylogenetic trees to model complex population-level relationships such as admixture or incomplete lineage sorting. Additionally, captions to Figure S3, do not explain colour-coding.  

We have removed “aBM tends to have long branches compare to tropicalis maize, which can be explained by adaption for specific local environment by time.” in our revised manuscript.

We have added the color-coding information under Fig. S3 in our revised manuscript.

(6) The conclusion that selection detected in aBM sample is due to Inca influence has no support. Firstly, selection signature can be due to environmental or other factors. To disentangle those, the authors would need to generate the data for a large number of samples from similar cultural contexts and from a wide-ranging environmental context, followed by a formal statistical test. Secondly, allele frequency increase can be attributed to selection or demographic processes, and alone is not sufficient evidence for selection. The presented XP-EHH method seems more suitable. Overall, methods used in this paper raise some concerns: i) how accurate are allele-frequency tests of selection when only single individual is used as a proxy for a whole population, ii) the significance threshold has been arbitrary fixed to an absolute number based on other studies, but the standard is to use, for example, top fifth percentile. Finally, linking selection to particular GO terms is not strong evidence, as correlation does not imply causation, and links are unclear anyway. 

In sum, this manuscript presents new data that seems to be of high quality, but the analyses are frequently inappropriate and/or over-interpreted. 

Regarding your suggestion that “from similar cultural contexts and from a wide-ranging environmental context, followed by a formal statistical test”, we apologize that this cannot be done in our current study because we could not find other archaeological maize samples/datasets that are from similar cultural contexts.

For “Secondly, allele frequency increase can be attributed to selection or demographic processes, and alone is not sufficient evidence for selection.” Yes, we agree, and that’s why we said it “inferred” the conclusion instead of “indicated”. Furthermore, we revised the whole manuscript following all reviewers’ comments and reorganized and reduced the part on selection on aBM.

For “The presented XP-EHH method seems more suitable”, we do not think XP-EHH is the best method that could be used here because we only have one aBM sample, but XP-EHH is more suitable for a population analysis.

For “Finally, linking selection to particular GO terms is not strong evidence, as correlation does not imply causation, and links are unclear anyway.”, as we described in our manuscript, our results “inferred” instead of “indicated” the conclusion.

Reviewer #2 (Public review): 

Summary: 

The manuscript presents valuable new datasets from two ancient maize seeds that contribute to our growing understanding of the maize evolution and biodiversity landscape in pre-colonial South America. Some of the analyses are robust, but the selection elements are not supported. 

Strengths: 

The data collection is robust, and the data appear to be of sufficiently high quality to carry out some interesting analytical procedures. The central finding that aBM maize is closely related to maize from the core Inca region is well supported, although the directionality of dispersal is not supported. 

Weaknesses: 

Thank you for your comments and suggestions. See below for responses and explanations.

The selection results are not justified, see examples in the detailed comments below. 

(1) The manuscript mentions cultural and natural selection (line 76), but then only gives a couple of examples of selecting for culinary/use traits. There are many examples of selection to tolerate diverse environments that could be relevant for this discussion, if desired. 

We have added related examples with references supported in our revised manuscript.  

(2) I would be extremely cautious about interpreting the observations of a Spanish colonizer (lines 95-99) without very significant caveats. Indigenous agriculture and food ways would have been far more nuanced than what could be captured in this context, and the genocidal activities of the Europeans would have impacted food production activities to a degree, and any contemporaneous accounts need to be understood through that lens.  

We agree with the first part of this comment and have softened our use of this particular textual material such that it is far less central to interpretation.While of interest, we cannot evaluate the impact of colonial European activities or observational bias for purposes of this analysis.

(3) The f3 stats presented in Figure 2 are not set up to test any specific admixture scenarios, so it is unsupported to conclude that the aBM maize is not admixed on this basis (lines 201-202). The original f3 publication (Patterson et al, 2012) describes some scenarios where f3 characteristics associate with admixture, but in general, there are many caveats to this approach, and it's not the ideal tool for admixture testing, compared with e.g., f4 and D (abba-baba) statistics.  

You make an important point that f3 stats is not the ideal tool for admixture testing. Since our study goal here is to identify which group(s) has(have) the highest relatedness with aBM, the population f3 statistic with an outgroup is the most robust metrics with which to do the test and to support our conclusion here. We have removed the “Our admixture f3-statistics test results suggest aBM is not admixed” in our revised manuscript.

(4) I'm a little bit skeptical that the Locator method adds value here, given the small training sample size and the wide geographic spread and genetic diversity of the ancient samples that include Central America. The paper describing that method (Battey et al 2020 eLife) uses much larger datasets, and while the authors do not specifically advise on sample sizes, they caution about small sample size issues. We have already seen that the ancient Peruvian maize has the most shared drift with aBM maize on the basis of the f3 stats, and the Locator analysis seems to just be reiterating that. I would advise against putting any additional weight on the Locator results as far as geographic origins, and personally I would skip this analysis in this case.  

As we described in our manuscript, we have 17 archaeological samples in total. Please find more detailed information from the “geographical location prediction” section.

We cannot add more ancient samples because they are all that we could find from all previous publications. We may still want to keep this analysis because f3 stats indicates the genome similarity, but the purpose of locator.py analysis is indicating the predicted location of origin of a genetic sample by comparing it to a set of samples of known geographic origin. 

(5) The overlap in PCA should not be used to confirm that aBM is authentically ancient, because with proper data handling, PCA placement should be agnostic to modern/ancient status (see lines 224-226). It is somewhat unexpected that the ancient Tehuacan maize (with a major teosinte genomic component) falls near the ancient South American maize, but this could be an artifact of sampling throughout the PCA and the lack of teosinte samples that might attract that individual.  

We have removed “which supports the authenticity of aBM as archaeological maize” in our revised manuscript. The PCA was only applied for all maize samples, so we did not include any teosinte samples in the analysis.

(6) What has been established (lines 250-251) is genetic similarity to the Inca core area, not necessarily the directionality. Might aBM have been part of a cultural region supplying maize to the Inca core region, for example? Without a specific test of dispersal directionality, which I don't think is possible with the data at hand, this is somewhat speculative. 

We added this and re-wrote this part in our revised manuscript.

(7) Singleton SNPs are not a typical criterion for identifying selection; this method needs some citations supporting the exact approach and validation against neutral expectations (line 278). Without Datasets S2 and S3, which are not included with this submission, it is difficult to assess this result further. However, it is very unexpected that ~18,000 out of ~49,000 SNPs would be unique to the aBM lineage. This most likely reflects some data artifact (unaccounted damage, paralogs not treated for high coverage, which are extremely prevalent in maize, etc). I'm confused about unique SNPs in this context. How can they be unique to the aBM lineage if the SNPs used overlap the Grzybowski set? The GO results do not include any details of the exact method used or a statistical assessment of the results. It is not clear if the GO terms noted are statistically enriched.  

We have added references 53 and 54 in our revised manuscript, and we also uploaded the Datasets S2 and S3.

For “I'm confused about unique SNPs in this context. How can they be unique to the aBM lineage if the SNPs used overlap the Grzybowski set?”, as we described in our materials and method part that “To achieve potential unique selection on aBM, we calculated the allele frequency for each SNPs between aBM and other archaeological maize, resulting in allele frequency data for 49,896 SNPs. Of these,18,668 SNPs were unique to aBM.”  Thus, the unique SNPs for aBM came from the comparison between aBM with other archaeological maize, and we did not use any modern maize data from the Grzybowski set.

For “The GO results do not include any details of the exact method used or a statistical assessment of the results. It is not clear if the GO terms noted are statistically enriched.” We did not do GO Term enrichment, so there are no statistical assessments for the results. What we have done was we retained the GO Terms information for each gene by checking their biological process from MaizeGDB, after that, we summarized the results in Dataset S4.

(8) The use of XP-EHH with pseudo haplotype variant calls is not viable (line 293). It is not clear what exact implementation of XP-EHH was used, but this method generally relies on phased or sometimes unphased diploid genotype calls to observe shared haplotypes, and some minimum population size to derive statistical power. No implementation of XP-EHH to my knowledge is appropriate for application to this kind of dataset. 

We used the same XP-EHH as this publication “Sabeti, P.C. et al. Genome-wide detection and characterization of positive selection in human populations. Nature 449, 913-918 (2007).” Specifically in our analysis, the SNP information of modern maize was compared with ancient maize. The code is available in https://doi.org/10.5061/dryad.w6m905qtd.

XP-EHH is a statistical method used in population genetics to detect recent positive selection in one population compared to another, and it often applied in modern large maize populations in previous research. In our study, we wanted to detect recent positive selection in modern maize compared to ancient maize, thus, we applied XP-EHH here. Although the population size of ancient maize is not big, it is the best method that we can apply for our dataset here to detect recent selection on modern maize.

Reviewer #3 (Public review): 

Summary: 

The authors seek to place archaeological maize samples (2 kernels) from Bolivia into genetic and geographical context and to assess signatures of selection. The kernels were dated to the end of the Incan empire, just prior to European colonization. Genetic data and analyses were used to characterize the distance from other ancient and modern maize samples and to predict the origin of the sample, which was discovered in a tomb near La Paz, Bolivia. Given the conquest of this region by the Incan empire, it is possible that the sample could be genetically similar to populations of maize in Peru, the center of the Incan empire. Signatures of selection in the sample could help reveal various environmental variables and cultural preferences that shaped maize genetic diversity in this region at that time. 

Strengths: 

The authors have generated substantial genetic data from these archaeological samples and have assembled a data set of published archaeological and modern maize samples that should help to place these samples in context. The samples are dated to an interesting time in the history of South America during a period of expansion of the Incan empire and just prior to European colonization. Much could be learned from even this small set of samples. 

Weaknesses: 

Many thanks for your comments and suggestions.  We have addressed these below and provided further explanation.

(1) Sample preparation and sequencing: 

Details of the quality of the samples, including the percentage of endogenous DNA are missing from the methods. The low percentage of mapped reads suggests endogenous DNA was low, and this would be useful to characterize more fully. Morphological assessment of the samples and comparison to morphological data from other maize varieties is also missing. It appears that the two kernels were ground separately and that DNA was isolated separately, but data were ultimately pooled across these genetically distinct individuals for analysis. Pooling would violate assumptions of downstream analysis, which included genetic comparison to single archaeological and modern individuals. 

We did not do the morphological assessment of the samples and comparison to morphological data from other maize varieties because we only have 2 aBM kernels, and we do not have other archaeological samples that could be used to do comparison.

For “It appears that the two kernels were ground separately and that DNA was isolated separately, but data were ultimately pooled across these genetically distinct individuals for analysis”, as you can see from our Materials and Methods section that “Whole kernels were crushed in a mortar and pestle”, these two kernels were ground together before sequenced. 

While morphological assessment of the sample would be interesting, most morphological data reported for maize are from microremains (starch, phytoliths, pollen) and this is beyond the scope of our study. Most studies of macrobotanical remains do not appear to focus solely on individual kernels, but instead on (or in combination with) cob and ear shape, which were not available in the assemblage.

(2) Genetic comparison to other samples: 

The authors did not meaningfully address the varying ages of the other archaeological samples and modern maize when comparing the genetic distance of their samples. The archaeological samples were as old as >5000 BP to as young as 70 BP and therefore have experienced varying extents of genetic drift from ancestral allele frequencies. For this reason, age should explicitly be included in their analysis of genetic relatedness. 

We have changed related part in our revised manuscript.

(3) Assessment of selection in their ancient Bolivian sample: 

This analysis relied on the identification of alleles that were unique to the ancient sample and inferred selection based on a large number of unique SNPs in two genes related to internode length. This could be a technical artifact due to poor alignment of sequence data, evidence supporting pseudogenization, or within an expected range of genetic differentiation based on population structure and the age of the samples. More rigor is needed to indicate that these genetic patterns are consistent with selection. This analysis may also be affected by the pooling of the Bolivian archaeological samples.  

We do not think it is because of poor alignment of sequence data since we used BWA v0.7.17 with disabled seed (-l 1024) and 0 mismatch alignment. Therefore, there are no SNPs that could come from poor alignment. Please see our detailed methods description here “For the archaeological maize samples, adapters were removed and paired reads were merged using AdapterRemoval60 with parameters --minquality 20 --minlength 30. All 5՛ thymine and 3՛ adenine residues within 5nt of the two ends were hard-masked, where deamination was most concentrated. Reads were then mapped to soft-masked B73 v5 reference genome using BWA v0.7.17 with disabled seed (-l 1024 -o 0 -E 3) and a quality control threshold (-q 20) based on the recommended parameter61 to improve ancient DNA mapping”.

For “More rigor is needed to indicate that these genetic patterns are consistent with selection”, Could you please be more specific about which method or approach we should use here? For example, methods from specific publications that could be referenced? Or which specific tool could be used?

“This analysis may also be affected by the pooling of the Bolivian archaeological samples.” As we could not prove these two seeds came from two different individual plants, we do not think this analysis was affected by the pooling of the Bolivian archaeological samples.

(4) Evidence of selection in modern vs. ancient maize: In this analysis, samples were pooled into modern and ancient samples and compared using the XP-EHH statistic. One gene related to ovule development was identified as being targeted by selection, likely during modern improvement. Once again, ancient samples span many millennia and both South, Central, and North America. These, and the modern samples included, do not represent meaningfully cohesive populations, likely explaining the extremely small number of loci differentiating the groups. This analysis is also complicated by the pooling of the Bolivian archaeological samples. 

Yes, it is possible that ovule development might be a modern improvement. We re-wrote this part in our revised manuscript.

Reviewer #1 (Recommendations for the authors): 

My suggestion is to address the comments that outline why the methods used or results obtained are not sufficient to support your conclusions. Overall, I suggest limiting the narrative of Inca influence and framing it as speculation in the discussion section. Presenting conclusions of Inca influence in the title and abstract is not appropriate, given the very questionable evidence. 

We agree and have changed the title to “Fifteenth century CE Bolivian maize reveals genetic affinities with ancient Peruvian maize”.

Reviewer #2 (Recommendations for the authors): 

(1) Line 74: Mexicana is another subspecies of teosinte; the distinction is between ssp. mexicana and ssp. parviglumis (Balsas teosinte), not mexicana and teosinte. 

We have corrected this in our revised manuscript.

(2) Line 100-102: This is a bit confusing, it cannot have been a symbol of empire "since its first introduction", since its introduction long predates the formation of imperial politics in the region. Reference 17 only treats the late precolonial Inca context, while ref 22 (which cites maize cultivation at 2450 BC, not 3000 BC) makes no reference to ritual/feasting contexts; it simply documents early phytolith evidence for maize cultivation. As such, this statement is not supported by the references offered.

lines 100-102. This point is well taken and was poor prose on our part.  We have modified this discussion to reflect both the confusing statement and we have corrected our mistake in age for reference 22. associated prose has been modified accordingly.

We have corrected them as “Indeed, in the Andes, previous research showed that under the Inca empire, maize was fulfilled multiple contextual roles. In some cases, it operated as a sacred crop” and “…since its first introduction to the region around 2500 BC”.

(3) Line 161: IntCal is likely not the appropriate calibration curve for this region; dates should probably be calibrated using SHCal.  

We greatly appreciate this important (and correct) observation. We have completely recalibrated the maize AMS result based on the southern hemisphere calibration curve, discussed the new calibrations, and have also invoked two other AMS dates also subjected to the southern hemisphere calibration on associated material for comparison.We are confident in a 15th century AD/CE age for the maize, most likely mid- to late 15th century.  

(4) Lines 167-169: The increase of G and A residues shown in Supplementary Figure S1a is just before the 5' end of the read within the reference genome context, and is related to fragmentation bias - a different process from postmortem deamination. Deamination leads to 5' C->T and 3' G->A, resulting in increased T at 5' ends and increased A at 3' ends, and the diagnostic damage curve. The reduction of C/T just before reads begin is not a result of deamination. 

We have removed the “Both features are indicative of postmortem deamination patterns” in our revised manuscript.

(5) Lines 187-196 This section presents a lot of important external information establishing hypotheses, and needs some references.  

We have added the related references here.

(6) Line 421: This makes it sound like damage masking was done BEFORE read mapping. However, this conflicts with the previous paragraph about map Damage, and Supplementary Figure 1 still shows a slight but perceptible damage curve, which is impossible if all terminal Ts and As are hard-masked. This should be reconciled.  

The Supplementary Figure 1 shows the raw ancient maize DNA sample before damage masking. Specifically, Step1: We used map Damage to check/estimate if the damage exists, and we made the Supplementary Figure 1. Step 2: Then we used our own code hard-masked the damage bases and did read mapping.

The purpose of Supplementary Figure 1 is to show the authenticity of aBM as archaeological maize. Therefore, it should show a slight but perceptible damage curve.

(7) Line 460: PCA method is not given (just the LD pruning and the plotting).  

The merged dataset of SNPs for archaeological and modern maize was used for PCA analysis by using “plink –pca”.

(8) "tropicalis" maize is not common usage, it is not clear to me what this refers to. 

We have changed all “tropicalis maize” as “tropical maize” in our revised manuscript.

(9) The Figure 4 color palette is not accessible for colorblind/color-deficient vision.  

We have changed the color of Figure 4. Please find the new colors in our upload Figure 4.

(10) Datasets S2 and S3 are not included with this submission. 

Thank you for letting us know and your suggestion. We have included Datasets S2 and S3 here.

Author response:

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

Public Reviews:

We thank the Reviewers for their thorough attention to our paper and the interesting discussion about the findings. Before responding to more specific comments, here some general points we would like to clarify:

(1) Ecological niche models are indeed correlative models, and we used them to highlight environmental factors associated with HPAI outbreaks within two host groups. We will further revise the terminology that could still unintentionally suggest causal inference. The few remaining ambiguities were mainly in the Discussion section, where our intent was to interpret the results in light of the broader scientific literature. Particularly, we will change the following expressions:

-  “Which factors can explain…” to  “Which factors are associated with…” (line 75);

-  “the environmental and anthropogenic factors influencing” to “the environmental and anthropogenic factors that are correlated with” (line 273);

-  “underscoring the influence” to “underscoring the strong association” (line 282).

(2) We respectfully disagree with the suggestion that an ecological niche modelling (ENM) approach is not appropriate for this work and the research question addressed therein. Ecological niche models are specifically designed to estimate the spatial distribution of the environmental suitability of species and pathogens, making them well suited to our research questions. In our study, we have also explicitly detailed the known limitations of ecological niche models in the Discussion section, in line with prior literature, to ensure their appropriate interpretation in the context of HPAI.

(3) The environmental layers used in our models were restricted to those available at a global scale, as listed in Supplementary Information Resources S1 (https://github.com/sdellicour/h5nx_risk_mapping/blob/master/Scripts_%26_data/SI_Resource_S1.xlsx). Naturally, not all potentially relevant environmental factors could be included, but the selected layers are explicitly documented and only these were assessed for their importance. Despite this limitation, the performance metrics indicate that the models performed well, suggesting that the chosen covariates capture meaningful associations with HPAI occurrence at a global scale.

Reviewer #1 (Public review):

The authors aim to predict ecological suitability for transmission of highly pathogenic avian influenza (HPAI) using ecological niche models. This class of models identify correlations between the locations of species or disease detections and the environment. These correlations are then used to predict habitat suitability (in this work, ecological suitability for disease transmission) in locations where surveillance of the species or disease has not been conducted. The authors fit separate models for HPAI detections in wild birds and farmed birds, for two strains of HPAI (H5N1 and H5Nx) and for two time periods, pre- and post-2020. The authors also validate models fitted to disease occurrence data from pre-2020 using post-2020 occurrence data. I thank the authors for taking the time to respond to my initial review and I provide some follow-up below.

Detailed comments:

In my review, I asked the authors to clarify the meaning of "spillover" within the HPAI transmission cycle. This term is still not entirely clear: at lines 409-410, the authors use the term with reference to transmission between wild birds and farmed birds, as distinct to transmission between farmed birds. It is implied but not explicitly stated that "spillover" is relevant to the transmission cycle in farmed birds only. The sentence, "we developed separate ecological niche models for wild and domestic bird HPAI occurrences ..." could have been supported by a clear sentence describing the transmission cycle, to prime the reader for why two separate models were necessary.

We respectfully disagree that the term “spillover” is unclear in the manuscript. In both the Methods and Discussion sections (lines 387-391 and 409-414), we explicitly define “spillover” as the introduction of HPAI viruses from wild birds into domestic poultry, and we distinguish this from secondary farm-to-farm transmission. Our use of separate ecological niche models for wild and domestic outbreaks reflects not only the distinction between primary spillover and secondary transmission, but also the fundamentally different ecological processes, surveillance systems, and management implications that shape outbreaks in these two groups. We will clarify this choice in the revised manuscript when introducing the separate models. Furthermore, on line 83, we will add “as these two groups are influenced by different ecological processes, surveillance biases, and management contexts”.

I also queried the importance of (dead-end) mammalian infections to a model of the HPAI transmission risk, to which the authors responded: "While spillover events of HPAI into mammals have been documented, these detections are generally considered dead-end infections and do not currently represent sustained transmission chains. As such, they fall outside the scope of our study, which focuses on avian hosts and models ecological suitability for outbreaks in wild and domestic birds." I would argue that any infections, whether they are in dead-end or competent hosts, represent the presence of environmental conditions to support transmission so are certainly relevant to a niche model and therefore within scope. It is certainly understandable if the authors have not been able to access data of mammalian infections, but it is an oversight to dismiss these infections as irrelevant.

We understand the Reviewer’s point, but our study was designed to model HPAI occurrence in avian hosts only. We therefore restricted our analysis to wild birds and domestic poultry, which represent the primary hosts for HPAI circulation and the focus of surveillance and control measures. While mammalian detections have been reported, they are outside the scope of this work.

Correlative ecological niche models, including BRTs, learn relationships between occurrence data and covariate data to make predictions, irrespective of correlations between covariates. I am not convinced that the authors can make any "interpretation" (line 298) that the covariates that are most informative to their models have any "influence" (line 282) on their response variable. Indeed, the observation that "land-use and climatic predictors do not play an important role in the niche ecological models" (line 286), while "intensive chicken population density emerges as a significant predictor" (line 282) begs the question: from an operational perspective, is the best (e.g., most interpretable and quickest to generate) model of HPAI risk a map of poultry farming intensity?

We agree that poultry density may partly reflect reporting bias, but we also assumed it a meaningful predictor of HPAI risk. Its importance in our models is therefore expected. Importantly, our BRT framework does more than reproduce poultry distribution: it captures non-linear relationships and interactions with other covariates, allowing a more nuanced characterisation of risk than a simple poultry density map. Note also that we distinguished in our models intensive and extensive chicken poultry density and duck density. Therefore, it is not a “map of poultry farming intensity”. 

At line 282, we used the word “influence” while fully recognising that correlative models cannot establish causality. Indeed, in our analyses, “relative influence” refers to the importance metric produced by the BRT algorithm (Ridgeway, 2020), which measures correlative associations between environmental factors and outbreak occurrences. These scores are interpreted in light of the broader scientific literature, therefore our interpretations build on both our results and existing evidence, rather than on our models alone. However, in the next version of the paper, we will revise the sentence as: “underscoring the strong association of poultry farming practices with HPAI spread (Dhingra et al., 2016)”. 

I have more significant concerns about the authors' treatment of sampling bias: "We agree with the Reviewer's comment that poultry density could have potentially been considered to guide the sampling effort of the pseudo-absences to consider when training domestic bird models. We however prefer to keep using a human population density layer as a proxy for surveillance bias to define the relative probability to sample pseudo-absence points in the different pixels of the background area considered when training our ecological niche models. Indeed, given that poultry density is precisely one of the predictors that we aim to test, considering this environmental layer for defining the relative probability to sample pseudo-absences would introduce a certain level of circularity in our analytical procedure, e.g. by artificially increasing to influence of that particular variable in our models." The authors have elected to ignore a fundamental feature of distribution modelling with occurrence-only data: if we include a source of sampling bias as a covariate and do not include it when we sample background data, then that covariate would appear to be correlated with presence. They acknowledge this later in their response to my review: "...assuming a sampling bias correlated with poultry density would result in reducing its effect as a risk factor." In other words, the apparent predictive capacity of poultry density is a function of how the authors have constructed the sampling bias for their models. A reader of the manuscript can reasonably ask the question: to what degree are is the model a model of HPAI transmission risk, and to what degree is the model a model of the observation process? The sentence at lines 474-477 is a helpful addition, however the preceding sentence, "Another approach to sampling pseudo-absences would have been to distribute them according to the density of domestic poultry," (line 474) is included without acknowledgement of the flow-on consequence to one of the key findings of the manuscript, that "...intensive chicken population density emerges as a significant predictor..." (line 282). The additional context on the EMPRES-i dataset at line 475-476 ("the locations of outbreaks ... are often georeferenced using place name nomenclatures") is in conflict with the description of the dataset at line 407 ("precise location coordinates"). Ultimately, the choices that the authors have made are entirely defensible through a clear, concise description of model features and assumptions, and precise language to guide the reader through interpretation of results. I am not satisfied that this is provided in the revised manuscript.

We thank the Reviewer for this important point. To address it, we compared model predictive performance and covariate relative influences obtained when pseudo-absences were weighted by poultry density versus human population density (Author response table 1). The results show that differences between the two approaches are marginal, both in predictive performance (ΔAUC ranging from -0.013 to +0.002) and in the ranking of key predictors (see below Author response images 1 and 2). For instance, intensive chicken density consistently emerged as an important predictor regardless of the bias layer used.

Note: the comparison was conducted using a simplified BRT configuration for computational efficiency (fewer trees, fixed 5-fold random cross-validation, and standardised parameters). Therefore, absolute values of AUC and variable importance may differ slightly from those in the manuscript, but the relative ranking of predictors and the overall conclusions remain consistent.

Given these small differences, we retained the approach using human population density. We agree that poultry density partly reflects surveillance bias as well as true epidemiological risk, and we will clarify this in the revised manuscript by noting that the predictive role of poultry density reflects both biological processes and surveillance systems. Furthermore, on line 289, we will add “We note, however, that intensive poultry density may reflect both surveillance intensity and epidemiological risk, and its predictive role in our models should be interpreted in light of both processes”.

Author response table 1.

Comparison of model predictive performances (AUC) between pseudo-absence sampling were weighted by poultry density and by human population density across host groups, virus types, and time periods. Differences in AUC values are shown as the value for poultry-weighted minus human-weighted pseudo-absences.

Author response image 1.

Comparison of variable relative influence (%) between models trained with pseudo-absences weighted by poultry density (red) and human population density (blue) for domestic bird outbreaks. Results are shown for four datasets: H5N1 (<2020), H5N1 (>2020), H5Nx (<2020), and H5Nx (>2020).

Author response image 2.

Comparison of variable relative influence (%) between models trained with pseudo-absences weighted by poultry density (red) and human population density (blue) for wild bird outbreaks. Results are shown for three datasets: H5N1 (>2020), H5Nx (<2020), and H5Nx (>2020).

The authors have slightly misunderstood my comment on "extrapolation": I referred to "environmental extrapolation" in my review without being particularly explicit about my meaning. By "environmental extrapolation", I meant to ask whether the models were predicting to environments that are outside the extent of environments included in the occurrence data used in the manuscript. The authors appear to have understood this to be a comment on geographic extrapolation, or predicting to areas outside the geographic extent included in occurrence data, e.g.: "For H5Nx post-2020, areas of high predicted ecological suitability, such as Brazil, Bolivia, the Caribbean islands, and Jilin province in China, likely result from extrapolations, as these regions reported few or no outbreaks in the training data" (lines 195-197). Is the model extrapolating in environmental space in these regions? This is unclear. I do not suggest that the authors should carry out further analysis, but the multivariate environmental similarly surface (MESS; see Elith et al., 2010) is a useful tool to visualise environmental extrapolation and aid model interpretation.

On the subject of "extrapolation", I am also concerned by the additions at lines 362-370: "...our models extrapolate environmental suitability for H5Nx in wild birds in areas where few or no outbreaks have been reported. This discrepancy may be explained by limited surveillance or underreporting in those regions." The "discrepancy" cited here is a feature of the input dataset, a function of the observation distribution that should be captured in pseudo-absence data. The authors state that Kazakhstan and Central Asia are areas of interest, and that the environments in this region are outside the extent of environments captured in the occurrence dataset, although it is unclear whether "extrapolation" is informed by a quantitative tool like a MESS or judged by some other qualitative test. The authors then cite Australia as an example of a region with some predicted suitability but no HPAI outbreaks to date, however this discussion point is not linked to the idea that the presence of environmental conditions to support transmission need not imply the occurrence of transmission (as in the addition, "...spatial isolation may imply a lower risk of actual occurrences..." at line 214). Ultimately, the authors have not added any clear comment on model uncertainty (e.g., variation between replicated BRTs) as I suggested might be helpful to support their description of model predictions.

Many thanks for the clarification. Indeed, we interpreted your previous comments in terms of geographic extrapolations. We thank the Reviewer for these observations. We will adjust the wording to further clarify that predictions of ecological suitability in areas with few or no reported outbreaks (e.g., Central Asia, Australia) are not model errors but expected extrapolations, since ecological suitability does not imply confirmed transmission (for instance, on Line 362: “our models extrapolate environmental suitability” will be changed to “Interestingly, our models extrapolate geographical”). These predictions indicate potential environments favorable to circulation if the virus were introduced.

In our study, model uncertainty is formally assessed when comparing the predictive performances of our models (Fig. S3, Table S1), the relative influence (Table S3) and response curves (Fig. 2) associated with each environmental factor (Table S2). All the results confirming a good converge between these replicates. Finally, we indeed did not use a quantitative tool such as a MESS to assess extrapolation but did rely on qualitative interpretation of model outputs.

All of my criticisms are, of course, applied with the understanding that niche modelling is imperfect for a disease like HPAI, and that data may be biased/incomplete, etc.: these caveats are common across the niche modelling literature. However, if language around the transmission cycle, the niche, and the interpretation of any of the models is imprecise, which I find it to be in the revised manuscript, it undermines all of the science that is presented in this work.

We respectfully disagree with this comment. The scope of our study and the methods employed are clearly defined in the manuscript, and the limitations of ecological niche modelling in this context are explicitly acknowledged in the Discussion section. While we appreciate the Reviewer’s concern, the comment does not provide specific examples of unclear or imprecise language regarding the transmission cycle, niche, or interpretation of the models. Without such examples, it is difficult to identify further revisions that would improve clarity.

Reviewer #2 (Public review):

The geographic range of highly pathogenic avian influenza cases changed substantially around the period 2020, and there is much interest in understanding why. Since 2020 the pathogen irrupted in the Americas and the distribution in Asia changed dramatically. This study aimed to determine which spatial factors (environmental, agronomic and socio-economic) explain the change in numbers and locations of cases reported since 2020 (2020--2023). That's a causal question which they address by applying correlative environmental niche modelling (ENM) approach to the avian influenza case data before (2015--2020) and after 2020 (2020--2023) and separately for confirmed cases in wild and domestic birds. To address their questions they compare the outputs of the respective models, and those of the first global model of the HPAI niche published by Dhingra et al 2016.

We do not agree with this comment. In the manuscript, it is well established that we are quantitatively assessing factors that are associated with occurrences data before and after 2020. We do not claim to determine the causality. One sentence of the Introduction section (lines 75-76) could be confusing, so we intend to modify it in the final revision of our manuscript. 

ENM is a correlative approach useful for extrapolating understandings based on sparse geographically referenced observational data over un- or under-sampled areas with similar environmental characteristics in the form of a continuous map. In this case, because the selected covariates about land cover, use, population and environment are broadly available over the entire world, modelled associations between the response and those covariates can be projected (predicted) back to space in the form of a continuous map of the HPAI niche for the entire world.

We fully agree with this assessment of ENM approaches.

Strengths:

The authors are clear about expected bias in the detection of cases, such geographic variation in surveillance effort (testing of symptomatic or dead wildlife, testing domestic flocks) and in general more detections near areas of higher human population density (because if a tree falls in a forest and there is no-one there, etc), and take steps to ameliorate those. The authors use boosted regression trees to implement the ENM, which typically feature among the best performing models for this application (also known as habitat suitability models). They ran replicate sets of the analysis for each of their model targets (wild/domestic x pathogen variant), which can help produce stable predictions. Their code and data is provided, though I did not verify that the work was reproducible.

The paper can be read as a partial update to the first global model of H5Nx transmission by Dhingra and others published in 2016 and explicitly follows many methodological elements. Because they use the same covariate sets as used by Dhingra et al 2016 (including the comparisons of the performance of the sets in spatial cross-validation) and for both time periods of interest in the current work, comparison of model outputs is possible. The authors further facilitate those comparisons with clear graphics and supplementary analyses and presentation. The models can also be explored interactively at a weblink provided in text, though it would be good to see the model training data there too.

The authors' comparison of ENM model outputs generated from the distinct HPAI case datasets is interesting and worthwhile, though for me, only as a response to differently framed research questions.

Weaknesses:

This well-presented and technically well-executed paper has one major weakness to my mind. I don't believe that ENM models were an appropriate tool to address their stated goal, which was to identify the factors that "explain" changing HPAI epidemiology.

Here is how I understand and unpack that weakness:

(1) Because of their fundamentally correlative nature, ENMs are not a strong candidate for exploring or inferring causal relationships.

(2) Generating ENMs for a species whose distribution is undergoing broad scale range change is complicated and requires particular caution and nuance in interpretation (e.g., Elith et al, 2010, an important general assumption of environmental niche models is that the target species is at some kind of distributional equilibrium (at time scales relevant to the model application). In practice that means the species has had an opportunity to reach all suitable habitats and therefore its absence from some can be interpreted as either unfavourable environment or interactions with other species). Here data sets for the response (N5H1 or N5Hx case data in domestic or wild birds ) were divided into two periods; 2015--2020, and 2020--2023 based on the rationale that the geographic locations and host-species profile of cases detected in the latter period was suggestive of changed epidemiology. In comparing outputs from multiple ENMs for the same target from distinct time periods the authors are expertly working in, or even dancing around, what is a known grey area, and they need to make the necessary assumptions and caveats obvious to readers.

We thank the Reviewer for this observation. First, we constrained pseudo-absence sampling to countries and regions where outbreaks had been reported, reducing the risk of interpreting non-affected areas as environmentally unsuitable. Second, we deliberately split the outbreak data into two periods (2015-2020 and 2020-2023) because we do not assume a single stable equilibrium across the full study timeframe. This division reflects known epidemiological changes around 2020 and allows each period to be modeled independently. Within each period, ENM outputs are interpreted as associations between outbreaks and covariates, not as equilibrium distributions. Finally, by testing prediction across periods, we assessed both niche stability and potential niche shifts. These clarifications will be added to the manuscript to make our assumptions and limitations explicit.

Line 66, we will add: “Ecological niche model outputs for range-shifting pathogens must therefore be interpreted with caution (Elith et al., 2010). Despite this limitation, correlative ecological niche models  remain useful for identifying broad-scale associations and potential shifts in distribution. To account for this, we analysed two distinct time periods (2015-2020 and 2020-2023).”

Line 123, we will revise “These findings underscore the ability of pre-2020 models in forecasting the recent geographic distribution of ecological suitability for H5Nx and H5N1 occurrences” to “These results suggest that pre-2020 models captured broad patterns of suitability for H5Nx and H5N1 outbreaks, while post-2020 models provided a closer fit to the more recent epidemiological situation”.

(3) To generate global prediction maps via ENM, only variables that exist at appropriate resolution over the desired area can be supplied as covariates. What processes could influence changing epidemiology of a pathogen and are their covariates that represent them? Introduction to a new geographic area (continent) with naive population, immunity in previously exposed populations, control measures to limit spread such as vaccination or destruction of vulnerable populations or flocks? Might those control measures be more or less likely depending on the country as a function of its resources and governance? There aren't globally available datasets that speak to those factors, so the question is not why were they omitted but rather was the authors decision to choose ENMs given their question justified? How valuable are insights based on patterns of correlation change when considering different temporal sets of HPAI cases in relation to a common and somewhat anachronistic set of covariates?

We agree that the ecological niche models trained in our study are limited to environmental and host factors, as described in the Methods section with the selection of predictors. While such models cannot capture causality or represent processes such as immunity, control measures, or governance, they remain a useful tool for identifying broad associations between outbreak occurrence and environmental context. Our study cannot infer the full mechanisms driving changes in HPAI epidemiology, but it does provide a globally consistent framework to examine how associations with available covariates vary across time periods.

(4) In general the study is somewhat incoherent with respect to time. Though the case data come from different time periods, each response dataset was modelled separately using exactly the same covariate dataset that predated both sets. That decision should be understood as a strong assumption on the part of the authors that conditions the interpretation: the world (as represented by the covariate set) is immutable, so the model has to return different correlative associations between the case data and the covariates to explain the new data. While the world represented by the selected covariates *may* be relatively stable (could be statistically confirmed), what about the world not represented by the covariates (see point 3)?

We used the same covariate layers for both periods, which indeed assumes that these environmental and host factors are relatively stable at the global scale over the short timeframe considered. We believe this assumption is reasonable, as poultry density, land cover, and climate baselines do not change drastically between 2015 and 2023 at the resolution of our analysis. We agree, however, that unmeasured processes such as control measures, immunity, or governance may have changed during this time and are not captured by our covariates.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

- Line 400-401: "over the 2003-2016 periods" has an extra "s"; "two host species" (with reference to wild and domestic birds) would be more precise as "two host groups".

- Remove comma line 404

Many thanks for these comments, we have modified the text accordingly.

Reviewer #2 (Recommendations for the authors):

Most of my work this round is encapsulated in the public part of the review.

The authors responded positively to the review efforts from the previous round, but I was underwhelmed with the changes to the text that resulted. Particularly in regard to limiting assumptions - the way that they augmented the text to refer to limitations raised in review downplayed the importance of the assumptions they've made. So they acknowledge the significance of the limitation in their rejoinder, but in the amended text merely note the limitation without giving any sense of what it means for their interpretation of the findings of this study.

The abstract and findings are essentially unchanged from the previous draft.

I still feel the near causal statements of interpretation about the covariates are concerning. These models really are not a good candidate for supporting the inference that they are making and there seem to be very strong arguments in favour of adding covariates that are not globally available.

We never claimed causal interpretation, and we have consistently framed our analyses in terms of associations rather than mechanisms. We acknowledge that one phrasing in the research questions (“Which factors can explain…”) could be misinterpreted, and we are correcting this in the revised version to read “Which factors are associated with…”. Our approach follows standard ecological niche modelling practice, which identifies statistical associations between occurrence data and covariates. As noted in the Discussion section, these associations should not be interpreted as direct causal mechanisms. Finally, all interpretive points in the manuscript are supported by published literature, and we consider this framing both appropriate and consistent with best practice in ecological niche modelling (ENM) studies.

We assessed predictor contributions using the “relative influence” metric, the terminology reported by the R package “gbm” (Ridgeway, 2020). This metric quantifies the contribution of each variable to model fit across all trees, rescaled to sum to 100%, and should be interpreted as an association rather than a causal effect.

L65-66 The general difficulty of interpreting ENM output with range-shifting species should be cited here to alert readers that they should not blithely attempt what follows at home.

I believe that their analysis is interesting and technically very well executed, so it has been a disappointment and hard work to write this assessment. My rough-cut last paragraph of a reframed intro would go something like - there are many reasons in the literature not to do what we are about to do, but here's why we think it can be instructive and informative, within certain guardrails.

To acknowledge this comment and the previous one, we revised lines 65-66 to: “However, recent outbreaks raise questions about whether earlier ecological niche models still accurately predict the current distribution of areas ecologically suitable for the local circulation of HPAI H5 viruses. Ecological niche model outputs for range-shifting pathogens must therefore be interpreted with caution (Elith et al., 2010). Despite this limitation, correlative ecological niche models  remain useful for identifying broad-scale associations and potential shifts in distribution.”

We respectfully disagree with the Reviewer’s statement that “_there are many reasons in the literature not to do what we are about to do”._ All modeling approaches, including mechanistic ones, have limitations, and the literature is clear on both the strengths and constraints of ecological niche models. Our manuscript openly acknowledges these limits and frames our findings accordingly. We therefore believe that our use of an ENM approach is justified and contributes valuable insights within these well-defined boundaries.

Reference: Ridgeway, G. (2007). Generalized Boosted Models: A guide to the gbm package. Update, 1(1), 2007.

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

Reviewer #1(Public review):

I am concerned by the authors' conceptualisation of "niche" within the manuscript. Is the "niche" we are modelling the niche of the pathogen itself? The niche of the (wild) bird host species as a group? The niche of HPAI transmission within (wild) bird host species (i.e., an intersection of pathogen and bird niches)? Or the niche of HPAI transmission in poultry? The precise niche being modelled should be clarified in the Introduction or early in the Methods of the manuscript. The first two definitions of niche listed above are relevant, but separate from the niche modelled in the manuscript - this should be acknowledged.

We acknowledge that these concepts were probably not enough clearly defined in the previous version of our manuscript, and we have now included an explicit definition in the fourth paragraph of the Introduction section: “We developed separate ecological niche models for wild and domestic bird HPAI occurrences, these models thus predicting the ecological suitability for the risk of local viral circulation leading to the detection of HPAI occurrences within each host group (rather than the niche of the virus or the host species alone).”

The authors should consider the precise transmission cycle involved in each HPAI case: "index cases" in farmed poultry, caused by "spillover" from wild birds, are relevant to the wildlife transmission cycle, while the ecological conditions coinciding with subsequent transmission in farmed poultry are likely to be fundamentally different. (For example, subsequent transmission is not conditional on the presence of wild birds.) Modelling these two separate, but linked, transmission cycles together may omit important nuances from the modelling framework.

We thank the Reviewer for highlighting the distinction between primary (wild-todomestic) and secondary (farm-to-farm) transmission cycles. Our modelling framework was designed to assess the ecological suitability of HPAI occurrences in wild and domestic birds separately. In the domestic poultry models, the response variables are the confirmed outbreaks data and do not distinguish between index cases resulting from primary or secondary infections.

One of the aims of the study is to evaluate the spatial distribution of areas ecologically suitable for local H5N1/x circulation either leading to domestic or wild bird cases, i.e. to identify environmental conditions where the virus may have persisted or spread, whether as a result of introduction by wild birds or farm-to-farm transmission. Introducing mechanistic distinctions in the response variable would not necessarily improve or affect the ecological suitability maps, since each type of transmission is likely to be associated with different covariates that are included in the models.

Also, the EMPRES-i database does not indicate whether each record corresponds to an index case or a secondary transmission event, so in practice it would not be possible to produce two different models. However, we agree that distinguishing between types of transmission is an interesting perspective for future research. This could be explored, for example, by mapping interfaces between wild and domestic bird populations or by inferring outbreak transmission trees using genomic data when available.

To avoid confusion, we now explicitly clarify this aspect in the Materials and Methods section: “It is important to note that the EMPRES-i database does not distinguish between index cases (e.g., primary spillover from wild birds) and secondary farm-to-farm transmissions. As such, our ecological niche models are trained on confirmed HPAI outbreaks in poultry that may result from different transmission dynamics — including both initial introduction events influenced by environmental factors and subsequent spread within poultry systems.”

We now also address this limitation in the Discussion section: “Finally, our models for domestic poultry do not distinguish between primary introduction events (e.g., spillover from wild birds) and secondary transmission between farms due to limitations in the available surveillance data. While environmental factors likely influence the risk of initial spillover events, secondary spread is more often driven by anthropogenic factors such as biosecurity practices and poultry trade, which are not included in our current modelling framework.”

The authors should clarify the meaning of "spillover" within the HPAI transmission cycle: if spillover transmission is from wild birds to farmed poultry, then subsequent transmission in poultry is separate from the wildlife transmission cycle. This is particularly relevant to the Discussion paragraph beginning at line 244: does "farm to farm transmission" have a distinct ecological niche to transmission between wild birds, and transmission between wild birds and farmed birds? And while there has been a spillover of HPAI to mammals, could the authors clarify that these detections are dead-end? And not represented in the dataset? Dhingra et al., 2016 comment on the contrast between models of "directly transmitted" pathogens, such as HPAI, and vector-borne diseases: for vector-borne diseases, "clear eco-climatic boundaries of vectors can be mapped", whereas "HPAI is probably not as strongly environmentally constrained". This is an important piece of nuance in their Discussion and a comment to a similar effect may be of use in this manuscript.

Following the Reviewer’s previous comment, we have now added clarifications in the Methods and Discussion sections defining spillover as the transmission of HPAI viruses from wild birds to domestic poultry (index cases), and secondary transmission as onward spread between farms. As mentioned in our answer above, we now emphasise that our models do not distinguish these dynamics, which are likely to be influenced by different drivers — ecological in the case of spillover, and often anthropogenic (e.g., poultry trade movement, biosecurity) in the case of farm-to-farm transmission.

The discussion regarding farm-to-farm transmission and spillovers is indeed an interpretation derived from the covariates analysis (see the second paragraph in the Discussion section). Specifically, we observed a stronger association between HPAI occurrences and domestic bird density after 2020, which may suggest that secondary infections (e.g., farm-to-farm transmission) became more prominent or more frequently reported. We however acknowledge that our data do not allow us to distinguish primary introductions from secondary transmission events, and we have added a sentence to explicitly clarify this: “However, this remains an interpretation, as the available data do not allow us to distinguish between index cases and secondary transmission events.”

We thank the Reviewer for raising the point of mammalian infections. While spillover events of HPAI into mammals have been documented, these detections are generally considered dead-end infections and do not currently represent sustained transmission chains. As such, they fall outside the scope of our study, which focuses on avian hosts and models ecological suitability for outbreaks in wild and domestic birds. However, we agree that future work could explore the spatial overlap between mammalian outbreak detections and ecological suitability maps for wild birds to assess whether such spillovers may be linked to localised avian transmission dynamics.

Finally, we have added a comment about the differences between pathogens strongly constrained by the environments and HPAI: “This suggests that HPAI H5Nx is not as strongly environmentally constrained as vector-borne pathogens, for which clear eco-climatic boundaries (e.g., vector borne diseases) can be mapped (Dhingra et al., 2016).” This aligns with the interpretation provided by Dhingra and colleagues (2016) and helps contextualise the predictive limitations of ecological niche models for directly transmitted pathogens like HPAI.

There are several places where some simple clarification of language could answer my questions related to ecological niches. For example, on line 74, "the ecological niche" should be followed by "of the pathogen", or "of HPAI transmission in wild birds", or some other qualifier that is most appropriate to the Authors' conceptualisation of the niche modelled in the manuscript. Similarly, in the following sentence, "areas at risk" could be followed by "of transmission in wild birds", to make the transmission cycle that is the subject of modelling clear to the reader. On line 83, it is not clear who or what is the owner of "their ecological niches": is this "poultry and wild birds", or the pathogen?

We agree with that suggestion and have now modified the related part of the text  accordingly (e.g., “areas at risk for local HPAI circulation” and “of HPAI in wild or domestic birds”).

I am concerned by the authors' treatment of sampling bias in their BRT modelling framework. If we are modelling the niche of HPAI transmission, we would expect places that are more likely to be subject to disease surveillance to be represented in the set of locations where the disease has been detected. I do not agree that pseudo-absence points are sampled "to account for the lack of virus detection in some areas" - this description is misleading and does not match the following sentence ("pseudo-absence points sampled ... to reflect the greater surveillance efforts ..."). The distribution of pseudo-absences should aim to capture the distribution of probable disease surveillance, as these data act as a stand-in for missing negative surveillance records. It is sensible that pseudo-absences for disease detection in wild birds are sampled proportionately to human population density, as the disease is detected in dead wild birds, which are more likely to be identified close to areas of human occupation (as stated on line 163). However, I do not agree that the same applies to poultry - the density of farmed poultry is likely to be a better proxy for surveillance intensity in farmed birds. Human population density and farmed poultry density may be somewhat correlated (i.e., both are low in remote areas), but poultry density is likely to be higher in rural areas, which are assumed to have relatively lower surveillance intensity under the current approach. The authors allude to this in the Discussion: "monitoring areas with high intensive chicken densities ... remains crucial for the early detection and management of HPAI outbreaks".

We agree with the Reviewer's comment that poultry density could have potentially been considered to guide the sampling effort of the pseudo-absences to consider when training domestic bird models. We however prefer to keep using a human population density layer as a proxy for surveillance bias to define the relative probability to sample pseudoabsence points in the different pixels of the background area considered when training our ecological niche models. Indeed, given that poultry density is precisely one of the predictors that we aim to test, considering this environmental layer for defining the relative probability to sample pseudo-absences would introduce a certain level of circularity in our analytical procedure, e.g. by artificially increasing to influence of that particular variable in our models.

Furthermore, it is also worth noting that, to better account for variations in surveillance intensity, we also adjusted the sampling effort by allocating pseudo-absences in proportion to the number of confirmed outbreaks per administrative unit (country or sub-national regions for Russia and China). This approach aimed to reduce bias caused by uneven reporting and surveillance efforts between regions. Additionally, we restricted model training to countries or regions with a minimum surveillance threshold (at least five confirmed outbreaks per administrative unit). Therefore, both presence and pseudo-absence points originated from areas with more consistent surveillance data.

We acknowledge in the Materials and Methods section that the approach proposed by the Reviewer could have been used: “Another approach to sampling pseudo-absences would have been to distribute them according to the density of domestic poultry.” Finally, our approach is also justified in our response to the next comment of the Reviewer.

Having written my review, including the paragraph above, I briefly scanned Dhingra et al., and found that they provide justification for the use of human population density to sample pseudoabsences in farmed birds: "the Empres-i database compiles outbreak locations data from very heterogeneous sources and in the absence of explicit GPS location data, the geo-referencing of individual cases is often through the use of place name gazetteers that will tend to force the outbreak location populated place, rather in the exact location of the farm where the disease was found, which would introduce a bias correlated with human population density." This context is entirely missing from the manuscript under review, however, I maintain the comment in the paragraph above - have the Authors trialled sampling pseudo-absences from poultry density layers?

We agree with the Reviewer’s comment and have now added this precision in the Materials and Methods section (in the third paragraph dedicated to ecological niche modelling): “However, as pointed out by Dhingra and colleagues (2016), the locations of outbreaks in the EMPRES-i database are often georeferenced using place name nomenclatures due to a lack of accurate GPS data, which could introduce a spatial bias towards populated areas.”

The authors indirectly acknowledge the role of sampling bias in model predictions at line 163, however, this point could be clearer: there is sampling bias in the set of locations where HPAI has been observed and failure to adequately replicate this sampling bias in pseudo-absence data could lead covariates that are correlated with the observation distribution to appear to be correlated with the target distribution. This point is alluded to but should be clearly acknowledged to allow the reader to appropriately interpret your results. I understand the point being made on line 163 is that surveillance of HPAI in wild birds has become more structured and less opportunistic over time - if this is the case, a statement to this effect could replace "which could influence earlier data sets", which is a little ambiguous. The Authors acknowledge the role of sampling bias in lines 241-242 - this may be a good place to remind the reader that they have attempted to incorporate sampling bias through the selection of their pseudoabsence dataset, particularly for wild bird models.

We thank the Reviewer for this comment. We have now clarified in the text that observed data on HPAI occurrence are inherently influenced by heterogeneous surveillance efforts and that failure to replicate this bias in pseudo-absence sampling could effectively lead to misleading correlations with covariates associated with surveillance effort rather than true ecological suitability. We have now rephrased the related sentence as follows: “This decline may indicate a reduced bias in observation data: typically, dead wild birds are more frequently found near human-populated areas due to opportunistic detections, whereas more recent surveillance efforts have become increasingly proactive (Giacinti et al., 2024).”

Dhingra et al. aimed to account for the effect of mass vaccination of birds in China. This does not appear to be included in the updated models - is this a relevant covariate to consider in updated models? Are the models trained on pre-2020 data predicting to post-2020 given the same presence dataset as previous models? It may be helpful to provide a comment on this if we consider the pre-2020 models in this work to be representative of pre-2020 models as a cohort. Given the framing of the manuscript as an update to Dhingra et al., it may be useful for the authors to briefly summarise any differences between the existing models and updated models. Dhingra et al., also examine spatial extrapolation, which is not addressed here. Environmental extrapolation may be a useful metric to consider: are there areas where models are extrapolating that are predicted to be at high risk of HPAI transmission? Finally, they also provide some inset panels on global maps of model predictions - something similar here may also be useful.

We thank the Reviewer for these comments. Vaccination coverage is indeed a relevant covariate for HPAI suitability in domestic birds. However, we did not include this variable in our updated models for two reasons. First, comprehensive vaccination data were only available for China, so it is not possible to include this variable in a global model. Second, available data were outdated and vaccination strategies can vary substantially over time.

We however agree with the Reviewer that the Materials and Methods section did not clarify clearly the differences with Dhingra et al. (2016), and we now detail these differences at the beginning of the Materials and Methods section: “Our approach is similar to the one implemented by Dhingra and colleagues (2016). While Dhingra et al. (2016) developed their models only for domestic birds over the 2003-2016 periods, our models were developed for two host species separately (wild and domestic birds) and for two time periods (2016-2020 and 2020-2023).”

We also detail the main difference concerning the pseudo-absences sampling:  Dhingra and colleagues (2016) used human population density to sample pseudo-absences to reflect potential surveillance bias and also account for spatial filtering (min/max distances from presence). We adopted a similar strategy but also incorporated outbreak count per country or province (in the case of China and Russia) into the pseudo-absence sampling process to further account for within-country surveillance heterogeneity. We have now added these specifications in the Materials and Methods section: “To account for heterogeneity in AIV surveillance and minimise the risk of sampling pseudo-absences in poorly monitored regions, we restricted our analysis to countries (or administrative level 1 units in China and Russia) with at least five confirmed outbreaks. Unlike Dhingra et al. (2016), who sampled pseudoabsences across a broader global extent, our sampling was limited to regions with demonstrated surveillance activity. In addition, we adjusted the density of pseudo-absence points according to the number of reported outbreaks in each country or admin-1 unit, as a proxy for surveillance effort — an approach not implemented in this previous study.”

We have now also provided a comparison between the different outputs, particularly in the Results section: “Our findings were overall consistent with those previously reported by Dhingra and colleagues (Dhingra et al., 2016), who used data from January 2004 to March 2015 for domestic poultry. However, some differences were noted: their maps identified higher ecological suitability for H5 occurrences before 2016 in North America, West Africa, eastern Europe, and Bangladesh, while our maps mainly highlight ecologically suitable regions in China, South-East Asia, and Europe (Fig. S5). In India, analyses consistently identified high ecologically suitable areas for the risk of local H5Nx and H5N1 circulation for the three time periods (pre-2016, 2016-2020, and post-2020). Similar to the results reported by Dhingra and colleagues, we observed an increase in the ecological suitability estimated for H5N1 occurrence in South America's domestic bird populations post-2020. Finally, Dhingra and colleagues identified high suitability areas for H5Nx occurrence in North America, which are predicted to be associated with a low ecological suitability in the 2016-2020 models.”

We acknowledge that some regions predicted as highly suitable correspond to areas where extrapolation likely occurs due to limited or no recorded outbreaks. We have now added these specifications when discussing the resulting suitability maps obtained for domestic birds: “For H5Nx post-2020, areas of high predicted ecological suitability, such as Brazil, Bolivia, the Caribbean islands, and Jilin province in China, likely result from extrapolations, as these regions reported few or no outbreaks in the training data”, and, for wild birds: “Some of the areas with high predicted ecological suitability reflect the result of extrapolations. This is particularly the case in coastal regions of West and North Africa, the Nile Basin, Central Asia (Kyrgyzstan, Tajikistan, Uzbekistan), Brazil (including the Amazon and coastal areas), southern Australia, and the Caribbean, where ecological conditions are similar to those in areas where outbreaks are known to occur but where records of outbreaks are still rare.”

For wild birds (H5Nx, post-2020), high ecological suitability was predicted along the West and North African coasts, the Nile basin, Central Asia (e.g., Kyrgyzstan, Tajikistan, Uzbekistan), the Brazilian coast and Amazon region, Caribbean islands, southern Australia, and parts of Southeast Asia. Ecological suitability estimated in these regions may directly result from extrapolations and should therefore be interpreted cautiously.

We also added a discussion of the extrapolation for wild birds (in the Discussion section): “Interestingly, our models extrapolate environmental suitability for H5Nx in wild birds in areas where few or no outbreaks have been reported. This discrepancy may be explained by limited surveillance or underreporting in those regions. For instance, there is significant evidence that Kazakhstan and Central Asia play a role as a centre for the transmission of avian influenza viruses through migratory birds (Amirgazin et al., 2022; FAO, 2005; Sultankulova et al., 2024). However, very few wild bird cases are reported in EMPRES-i. In contrast, Australia appears environmentally suitable in our models, yet no incursion of HPAI H5N1 2.3.4.4b has occurred despite the arrival of millions of migratory shorebirds and seabirds from Asia and North America. Extensive surveillance in 2022 and 2023 found no active infections nor evidence of prior exposure to the 2.3.4.4b lineage (Wille et al., 2024; Wille and Klaassen, 2023).”

We agree that inset panels can be helpful for visualising global patterns. However, all resulting maps are available on the MOOD platform (https://app.mood-h2020.eu/core), which provides an interactive interface allowing users to zoom in and out, identify specific locations using a background map, and explore the results in greater detail. This resource is referenced in the manuscript to guide readers to the platform.

Related to my review of the manuscript's conceptualisation above, there are several inconsistencies in terminology in the manuscript - clearing these up may help to make the methods and their justification clearer to the reader. The "signal" that the models are estimating is variously described as "susceptibility" and "risk" (lines 179-180), "HPAI H5 ecological suitability" (line 78), "likelihood of HPAI occurrences" (line 139), "risk of HPAI circulation" (line 187), "distribution of occurrence data" (line 428). Each of these quantities has slightly different meanings and it is confusing to the reader that all of these descriptors are used for model output. "Likelihood of HPAI occurrences" is particularly misleading: ecological niche models predict high suitability for a species in areas that are similar to environments where it has previously been identified, without imposing constraints on species movement. It is intuitively far more likely that there will be HPAI occurrences in areas where the disease is already established than in areas where an introduction event is required, however, the niche models in this work do not include spatial relationships in their predictions.

We agree with the Reviewer’s comments. We have now modified the text so that in the Results section we refer to ecological suitability when referring to the outputs of the models. In the context of our Discussion section, we then interpret this ecological suitability in terms of risk, as areas with high ecological suitability being more likely to support local HPAI outbreaks.

I also caution the authors in their interpretation of the results of BRTs, which are correlative models, so therefore do not tell us what causes a response variable, but rather what is correlated with it. On Line 31, "correlated with" may be more appropriate than "influenced by". On Line 82, "correlated with" is more appropriate than "driving". This is particularly true given the authors' treatment of sampling bias.

We agree with the Reviewer’s comment and have now rephrased these sentences as follows: “The spatial distribution of HPAI H5 occurrences in wild birds appears to be primarily correlated with urban areas and open water regions” and “Our results provide a better understanding of HPAI dynamics by identifying key environmental factors correlated with the increase in H5Nx and H5N1 cases in poultry and wild birds, investigating potential shifts in their ecological niches, and improving the prediction of at-risk areas.”

The following sentences in line 201 are ambiguous: "For both H5Nx and H5N1, however, isolated areas on the risk map should be interpreted with caution. These isolated areas may result from sparse data, model limitations, or local environmental conditions that may not accurately reflect true ecological suitability." By "isolated", do the authors mean remote? Or ecologically dissimilar from the set of locations where HPAI has been detected? Or ecologically dissimilar from the set of locations in the joint set of HPAI detection locations and pseudo-absences? Or ecologically similar to the set of locations where HPAI has been detected but spatially isolated? These four descriptors are each slightly different and change the meaning of the sentences. "Model limitations" are also ambiguous - could the authors clarify which specific model limitations they are referring to here? Ultimately, the point being made is probably that a model may predict high ecological suitability for HPAI transmission in areas where the disease has not yet been identified, or where a model is extrapolating in environmental space, however, uncertainty in these predictions may be greater than uncertainty in predictions in areas that are represented in surveillance data. A clear comment on model uncertainty and how it is related to the surveillance dataset and the covariate dataset is currently missing from the manuscript and would be appropriate in this paragraph.

We understand the Reviewer’s concerns regarding these potential ambiguities, and have now rephrased these sentences as follows: “For both H5Nx and H5N1, certain areas of predicted high ecological suitability appear spatially isolated, i.e. surrounded by regions of low predicted ecological suitability. These areas likely meet the environmental conditions associated with past HPAI occurrences, but their spatial isolation may imply a lower risk of actual occurrences, particularly in the absence of nearby outbreaks or relevant wild bird movements.”

I am concerned by the wording of the following sentence: "The risk maps reveal that high-risk areas have expanded after 2020" (line 203). This statement could be supported by an acknowledgement of the assumptions the models make of the HPAI niche: are we saying that the niche is unchanged in environmental space and that there are now more geographic areas accessible to the pathogen, or that the niche has shifted or expanded, and that there are now more geographic areas accessible to the pathogen? The authors should review the sentence beginning on line 117: if models trained on data from the old timepoint predicting to the new timepoint are almost as good as models trained on data from the new timepoint predicting to the new timepoint, doesn't this indicate that the niche, as the models are able to capture it, has not changed too much?

We thank the Reviewer for this comment. The statement that "high-risk areas have expanded after 2020" indeed refers to an increase in the geographic extent of areas predicted to have high ecological suitability in models trained on post-2020 data. This expansion likely reflects new outbreak data from regions that had not previously reported cases, which in turn influenced model training.

However, models trained on pre-2020 data retain reasonable predictive performance when applied to post-2020 data (see the AUC results reported in Table S1), suggesting that the models suggest an expansion in the ecological suitability, but do not provide definitive evidence of a shift in the ecological niche. We have now added a statement at the end of this paragraph to clarify this point: “However, models trained on pre-2020 data maintained reasonable predictive performance when tested on post-2020 data, suggesting that the overall ecological niche of HPAI did not drastically shift over time.”

The final two paragraphs of the Results might be more helpful to include at the beginning of the Results, as the data discussed there are inputs to the models. Is it possible that the "rise in Shannon index for sea birds" that "suggests a broadening of species diversity within this category from 2020 onwards" is caused by the increasingly structured surveillance of HPAI in wild birds alluded to earlier in the Results? Is the "prevalence" discussed in line 226 the frequency of the families Laridae and Sulidae being represented in HPAI detection data? Or the abundance of the bird species themselves? The language here is a little ambiguous. Discussion of particular values of Shannon/Simpson indices is slightly out of context as the meanings of the indices are in the Methods - perhaps a brief explanation of the uses of Shannon/Simpson indices may be helpful to the reader here. It may also be helpful to readers who are not acquainted with avian taxonomy to provide common names next to formal names (for example, in brackets) in the body of the text, as this manuscript is published in an interdisciplinary journal.

We thank the Reviewer for these comments. First, we acknowledge that the paragraphs on species diversity and Shannon/Simpson indices describe important data, but we have chosen to present them after the main modelling results in order to maintain a logical narrative flow. Our manuscript first presents the ecological niche models and their predictive performance, followed by interpretations of the observed patterns, including changes in avian host diversity. Diversity indices were used primarily to support and contextualise the patterns observed in the modelling results.

For clarity, we have revised the relevant paragraphs in the Results (i) to briefly remind readers of the interpretation of the Shannon and Simpson indices (“Note that these indices reflect the diversity of bird species detected in outbreak records, not necessarily their abundance in the wild”) and (ii) to clarify that “prevalence” refers to the frequency of HPAI detection in wild bird species of the Laridae (gulls) and Sulidae (boobies and gannets) families, and not their total abundance. Family of birds includes several species, so the “common name” of a family can sometimes refer to species from other families. We have now added the common names for each family in the manuscript (even if we indeed acknowledge that “penguins” can be ambiguous).

In the Methods, it is stated: "To address the heterogeneity of AIV surveillance efforts and to avoid misclassifying low-surveillance areas as unsuitable for virus circulation, we trained the ecological niche models only considering countries in which five or more cases have been confirmed." However, it is not clear how this processing step prevents low-surveillance areas from being misclassified. If pseudo-absences are appropriately sampled, low-surveillance areas should be less represented in the pseudo-absence dataset, which should lead the models to be uncertain in their predictions of these areas. Perhaps "To address the heterogeneity of AIV surveillance efforts and to avoid sampling pseudo-absence data in realistically low-surveillance areas" is a more accurate introduction to the paragraph. I am not entirely convinced that it is appropriate to remove detection data where the national number of cases is low. This may introduce further sampling bias into the dataset.

We take the opportunity of the Reviewer’s comment to further clarify this important step aiming to mitigate bias associated with countries with substantial uncertainty in reporting and/or potentially insufficient HPAI surveillance data. While we indeed acknowledge that this procedure may exclude countries that had effective surveillance but low virus detection, we argue that it constitutes a relevant conservative approach to minimising the risk of sampling a significant number of pseudo-absence points in areas associated with relatively high yet undetected local HPAI circulation due to insufficient surveillance. Furthermore, given that five cases over two decades is a relatively low threshold — particularly for a highly transmissible virus such as AIV — non-detection or non-reporting remains a more plausible explanation than true absence.

To improve clarity, we have now revised the related sentence as follows: “To account for heterogeneity in AIV surveillance and minimise the risk of sampling pseudo-absences in poorly monitored regions, we restricted our analysis to countries (or administrative level 1 units in China and Russia) with at least five confirmed outbreaks.”

The reporting of spatial and temporal resolution of data in the manuscript could be significantly clearer. Is there a reason why human population density is downscaled to 5 arcminutes (~10km at the equator) while environmental covariate data has a resolution of 1km? The projection used is not reported. The authors should clarify the time period/resolution of the covariate data assigned to the occurrence dataset, for example, does "day LST annual mean" represent a particular year pre- or post-2020? Or an average over a number of years? Given that disease detections are associated with observation and reporting dates, and that there may be seasonal patterns in HPAI occurrence, it would be helpful to the reader to include this information when the eco-climatic indices are described. It would also be helpful to the reader to summarise the source, spatial and temporal resolution of all covariates in a table, as in Dhingra et al. Could the Authors clarify whether the duck density layer is farmed ducks or wild ducks?

The projection is WGS 84 (EPSG:4326) and the resolution of the output maps is around 0.0833 x 0.0833 decimal degrees (i.e. 5 arcmin, or approximately 10 km at the equator). We have now added these specifications in the text: “All maps are in a WGS84 projection with a spatial resolution of 0.0833 decimal degrees (i.e. 5 arcmin, or approximately 10 km at the equator).” In addition, we have now specified in the text that duck refers to domestic duck for clarity. 

Environmental variables retrieved for our analyses were here available as values averaged over distinct periods of time (for further detail see Supplementary Information Resources S1 — description and source of each environmental variable included in the original sets of variables — available at https://github.com/sdellicour/h5nx_risk_mapping). In future works, this would indeed be interesting to associate the occurrences to a specific season with the variables accordingly, specially for viruses such as HPAI which have been found correlated with seasons. However, we did not conduct this type of analysis in the present study, occurrences being here associated with averaged values of environmental data only.

In line 407, the authors state a number of pseudo-absence points used in modelling, relative to the number of presence points, without clear justification. Note that relative weights can be assigned to occurrence data in most ECN software (e.g., R package gbm), to allow many pseudo-absence points to be sampled to represent the full extent of probable surveillance effort and subsequently down-weighted.

We thank the Reviewer for this suggestion. We acknowledge that alternative approaches such as down-weighting pseudo-absence points could offer a certain degree of flexibility in representing surveillance effort. However, we opted for a fixed 1:3 ratio of pseudoabsences to presence points within each administrative unit to ensure a consistent and conservative sampling distribution. This approach aimed to limit overrepresentation of pseudoabsences in areas with sparse presence data, while still reflecting areas of likely surveillance.

There are a number of typographical errors and phrasing issues in the manuscript. A nonexhaustive list is provided below.

- Line 21: "its" should be "their" - Line 25: "HPAI cases"

Modifications have been done.

- Line 63: sentence beginning "However" is somewhat out of context - what is it (briefly) about recent outbreaks that challenge existing models?

We have now edited that sentence as follows: “However, recent outbreaks raise questions about whether earlier ecological niche models still accurately predict the current distribution of areas ecologically suitable for the local circulation of HPAI H5 viruses.”

- Lines 71 and 390: "AIV" is not defined in the text - Line 73: "do" ("are" and "what" are not capitalised)

Modifications have been done.

- Line 115: "predictability" should be "predictive capacity"

We have now replaced “predictability” by “predictive performance”.

- Line 180: omit "pinpointing"

- Line 192 sentence beginning "In India," should be re-worded: is the point that there are detections of HPAI here and the model predicts high ecological suitability?

- Line 195 sentence beginning "Finally," phrasing could be clearer: Dhingra et al. find high suitability areas for H5Nx in North America which are predicted to be low suitability in the new model.

- Line 237: omit "the" in "with the those"

- Line 374: missing "."

- Line 375: "and" should be "to" (the same goes for line 421)

- Line 448: Rephrase "Simpson index goes" to "The Simpson index ranges"

Modifications have been done.

Reviewer #2 (Public Review):

What is the justification for separating the dataset at 2020? Is it just the gap in-between the avian influenza outbreaks?

We chose 2020 as a cut-off based on a well-documented shift in HPAI epidemiology, notably the emergence and global spread of clade 2.3.4.4b, which may affect host dynamics and geographic patterns. We have now added this precision in the Materials and Methods section: “We selected 2020 as a cut-off point to reflect a well-documented shift in HPAI epidemiology, notably the emergence and global spread of clade 2.3.4.4b. This event marked a turning point in viral dynamics, influencing both the range of susceptible hosts and the geographical distribution of outbreaks.”

If the analysis aims to look at changing case numbers and distribution over time, surely the covariate datasets should be contemporaneous with the response?

Thank you for raising this important point. While we acknowledge that, ideally, covariates should match the response temporally, such high-resolution spatiotemporal environmental data were not available for most environmental factors considered in our ecological niche modelling analyses. While we used predictors (e.g., land-use variables, poultry density) that reflect long-term ecological suitability, we acknowledge that rather considering short-term seasonal variation could be an interesting perspective in future works, which is now explicitly stated in the Discussion section: “In addition, aligning outbreak occurrences with seasonally matched environmental variables could further refine predictions of HPAI risk linked to migratory dynamics.”

I would expect quite different immunity dynamics between domestic and wild birds as a function of lifespan and birth rates - though no obvious sign of that in the raw data. A statement on assumptions in that respect would be good.

Thank you for the comment. We agree that domestic and wild birds likely exhibit different immunity dynamics due to differences in lifespan, turnover rates, and exposure. However, our analyses did not explicitly model immunity processes, and the data did not show a clear signal of these differences.

Decisions and analytical tactics from Dhingra et al are adopted here in a way that doesn't quite convey the rationale, or justify its use here.

We thank the Reviewer for this observation. However, we do not agree with the notion that the rationale for using Dhingra et al.’s analytical framework is insufficiently conveyed. We adapted key components of their ecological niche modelling approach — such as the use of a boosted regression tree methodology and pseudo-absences sampling procedure — to ensure comparability with their previous findings, while also extending the analysis to additional time periods and host categories (wild vs. domestic birds). This framework aligns with the main objective of our study, which is to assess shifts in ecological suitability for HPAI over time and across host species, in light of changing viral dynamics.  

Please go over the manuscript and harmonise the language about the model target - it is usually referred to as cases, but sometimes the pathogen, and others the wild and domestic birds where the cases were discovered.

We agree and we have now modified the text to only use the “cases” or “occurrences” terminology when referring to the model inputs.

Is the reporting of your BRT implementation correct? The text suggests that only 10 trees were run per replicate (of which there were 10 per response (domestic/wild x H5N1 / H5Nx) x distinct covariate set), but this would suggest that the authors were scarcely benefiting from the 'boosting' part of the BRTs that allow them to accurately estimate curvilinear functions. As additional trees are added, they should still be improving the loss function, and dramatically so in the early stages. The authors seem heavily guided by Elith et al's excellent paper[1] explaining BRTs and the companion tutorial piece, but in that work, the recommended approach is to run an initial model with a relatively quick learning rate that achieves the best fit to the held-out data at somewhere over 1000 trees, and then to refine the model to that number of trees with a slower learning rate. If the authors did indeed run only 10 trees I think that should be explained.

For each model, we used the “gbm.step” function to fit boosted regression trees, initiating the process with 10 trees and allowing up to 10,000 trees in steps of 5. The optimal number of trees was automatically determined by minimising the cross-validated deviance, following the recommended approach of Elith and colleagues (2008, J. Anim. Ecol.). This setup allows the boosting algorithm to iteratively improve model performance while avoiding overfitting. These aspects are now further clarified in the Materials and Methods section: “All BRT analyses were run and averaged over 10 cross-validated replicates, with a tree complexity of 4, a learning rate of 0.01, a tolerance parameter of 0.001, and while considering 5 spatial folds. Each model was initiated with 10 trees, and additional trees were incrementally added (in steps of 5) up to a maximum of 10,000, with the optimal number selected based on cross-validation tests.”

I'm uncomfortable with the strong interpretation of changes in indices such as those for diversity in the case of bird species with detected cases of avian influenza, and the relative influence of covariates in the environmental niche models. In the former case, if surveillance effort is increasing it might be expected that more species will be found to be infected. In the latter, I'm just not convinced that these fundamentally correlative models can support the interpretation of changing epidemiology as asserted by authors. This strikes me as particularly problematic in light of static and in some cases anachronistic predictor sets.

We thank the Reviewer for drawing attention to how changes in surveillance intensity might influence our diversity estimates. We have now integrated a new analysis to evaluate the increase in the number of wild birds tested and discussed the potential impact of this increase on the comparison of the bird species diversity metrics presented in our study, which is now interpreted with more caution: “To evaluate whether the post-2020 increase in species diversity estimated for infected wild birds could result from an increase in the number of tests performed on wild birds, we compared European annual surveillance test counts (EFSA et al., 2025, 2019) before and after 2020 using a Wilcoxon rank-sum test. We relied on European data because it was readily accessible and offered standardised and systematically collected metrics across multiple years, making it suitable for a comparative analysis. Although borderline significant (p-value = 0.063), the Wilcoxon rank-sum test indeed highlighted a recent increase in the number of wild bird tests (on average >11,000/year pre-2020 and >22,000 post-2020), which indicates that the comparison of bird species diversity metrics should be interpreted with caution. However, such an increase in the number of tests conducted in the context of a passive surveillance framework would thus also be in line with an increase in the number of wild birds found dead and thus tested. Therefore, while the increase in the number of tests could indeed impact species diversity metrics such as the Shannon index, it can also reflect an absolute higher wild bird mortality in line with a broadened range of infected bird species.”

Author response:

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

Reviewer #1 (Public review):

(1) The authors devote significant effort to characterizing the physical interaction between Bicc1 and Pkd2. However, the study does not examine or discuss how this interaction relates to Bicc1's well-established role in posttranscriptional regulation of Pkd2 mRNA stability and translation efficiency.

The reviewer is correct that the present study has not addressed the downstream consequences of uthis interaction considering that Bicc1 is a posttranscriptional regulator of Pkd2 (and potentially Pkd1). We think that the complex of Bicc1/Pkd1/Pkd2 retains Bicc1 in the cytoplasm and thus restrict its activity in participating in posttranscriptional regulation (see Author response image 1). We, however, do not yet have data to support this and thus have not included this model in the manuscript. Yet, we have updated the discussion of the manuscript to further elaborate on the potential mechanism of the Bicc1/Pkd1/Pkd2 complex.

We have updated the discussion to include a discussion on the potential consequences on posttranscriptional regulation by Bicc1.

Author response image 1.

Model of BICC1, PC1 and PC2 self-regulation. In this model Bicc1 acts as a positive regulator of PKD gene expression. In the presence of ‘sufficient’ amounts of PC1/PC2 complex, it is tethered to the complex and remains biologically inactive (Fig. 1A). However, once the levels of the PC1/PC2 complex are reduced, Bicc1 is now present in the cytoplasm to promote expression of the PKD proteins, thereby raising their levels (Fig. 4B), which then in turn will ‘shutdown’ Bicc1 activity by again tethering it to the plasma membrane.

(2) Bicc1 inactivation appears to downregulate Pkd1 expression, yet it remains unclear whether Bicc1 regulates Pkd1 through direct interaction or by antagonizing miR-17, as observed in Pkd2 regulation. This should be further examined or discussed.

This is a very interesting comment. Vishal Patel published that PKD1 is regulated by a mir-17 binding site in its 3’UTR (PMID: 35965273). We, however, have not evaluated whether BICC1 participates in this regulation. A definitive answer would require utilization of the mice described in above reference, which is beyond the scope of this manuscript. We, however, have revised the discussion to elaborate on this potential mechanism. 

We have updated the discussion to include a statement on the potential direct regulation of Pkd1 mRNA by Bicc1.

(3) The evidence supporting Bicc1 and ADPKD gene cooperativity, particularly with Pkd1, in mouse models is not entirely convincing, likely due to substantial variability and the aggressive nature of Bpk/Bpk mice. Increasing the number of animals or using a milder Bicc1 strain, such as jcpk heterozygotes, could help substantiate the genetic interaction.

We have initially performed the analysis using our Bicc1 complete knockout, we previously reported on (PMID 20215348) focusing on compound heterozygotes. Yet, similar to the Pkd1/Pkd2 compound heterozygotes (PMID 12140187) no cyst development was observed when we sacrificed the mice as late as P21. Our strain is similar to the above mentioned jcpk, which is characterized by a short, abnormal transcript thought to result in a null allele (PMID: 12682776). We thank the reviewer for pointing us to the reference showing the heterozygous mice exhibit glomerular cysts in the adults (PMID: 7723240). This suggestion is an interesting idea we will investigate. In general, we agree with the reviewer that a better understanding of the contribution of Bicc1 to the adult PKD phenotype will be critical. To this end, we are currently generating a floxed allele of Bicc1 that will allow us to address the cooperativity in the adult kidney, when e.g. crossed to the Pkd1^RC/RC mice. Yet, these experiments are beyond the timeframe for this revision. 

No changes were made in the revised manuscript. 

Reviewer #2 (Public review):

(1) These results are potentially interesting, despite the limitation, also recognized by the authors, that BICC1 mutations seem exceedingly rare in PKD patients and may not "significantly contribute to the mutational load in ADPKD or ARPKD". The manuscript has several intrinsic limitations that must be addressed. 

As mentioned above, the study was designed to explore whether there is an interaction between BICC1 and the PKD1/PKD2 and whether this interaction is functionally important. How this translates into the clinical relevance will require additional studies (and we have addressed this in the discussion of the manuscript).

(2) The manuscript contains factual errors, imprecisions, and language ambiguities. This has the effect of making this reviewer wonder how thorough the research reported and analyses have been. 

We respectfully disagree with the reviewer on the latter interpretation. The study was performed with rigor. We have carefully assessed the critiques raised by the reviewer. As presented below, most of the criticisms raised by the reviewer have been easily addressed in the revised version of the manuscript. Yet, none of the critiques seems to directly impact the overall interpretation of the data. 

Reviewer #1 (Recommendations for the authors):

(1) The manuscript requires further editing. For example, figure panels and legends are mismatched in Figure 1

We have corrected the labeling of Figure 1. 

(2) Y-axis units and values are inconsistent in Figures 4b-4g, Supplementary Figures S2e and S2f are not referenced in the text, genotypes are missing in Supplementary Figure S3f, and numerous typographical errors are present.

In respect to the y-axis in Figure 4b-g, the scale is different for each of them, but that is intentional as one would lose the differences if they were all scaled identically. But we have now mentioned this in the figure legend to make the reader aware of it. In respect to the Supplemental Figure S2e,f, we included the panels in the description of the mutant BICC1 lines, but unfortunately forgot to reference them. This has now been done.

We have updated the labeling of the Y-axis for the cystic indices adding “[%]” as the unit and updated the figure legend of Figure 4. We have included the genotypes in Supplementary Figure S3f. The Supplementary Figure S2e,f is now mentioned in the supplemental material (page 9, 2^nd paragraph). 

Reviewer #2 (Recommendations for the authors):

(1) Previous data from mouse, Xenopus, and zebrafish suggest a crucial role for the RNAbinding protein Bicc1 in the pathogenesis of PKD, although BICC1 mutations in human PKD have not been previously reported." The cited sources (and others that were not cited) link Bicc1 mutations to renal cysts, similar to a report by Kraus (PMID: 21922595) that the authors cite later. However, a more direct link to PKD was reported by Lian and colleagues using whole Pkd1 mice (PMID: 20219263) and by Gamberi and colleagues using Pkd1 kidneys and human microarrays (PMID: 28406902). Although relevant, neither is cited here, and only the former is cited later in the manuscript.

Thanks for pointing this out. We have added these three citations.

We have added these three citations (PMID: 21922595, PMID: 20219263 and PMID: 28406902) in the indicated sentence.

(2) In Figure 1B, the lanes do not seem to correspond among panels, particularly evident in the panel with myc-mBicc1. Hence, it is difficult to agree with the presented conclusions.

We have corrected the labeling of the lanes in Figure 1b.

(3) In the Figure 1 legend: "(g) Western blot analysis following co-IP experiments, using an anti-mouse Bicc1 or anti-goat PC2 antibody as bait, identified protein interactions between endogenous PC2 and BICC1 in UCL93 cells. Non-immune goat and mouse IgG were included as a negative control." There is no mention of panel H, although this reviewer can imagine what the authors meant. The capitalization differs in the figure and legend. More troublingly, in panel G, a non-defined star indicates a strong band present in both immune and non-immune control.

We have corrected the figure legend of Figure 1 and clarified the non-specific band in the figure legend.

(4) In Figure 4, the authors do not show the matched control for the Bicc1 Pkd1 interaction in panel d, nor do they show a scale bar in either a) or d). Thus, the phenotypic severity cannot be properly assessed.

Thanks for pointing out the missing scale bars, which have now been added. In respect to the two kidneys shown in Figure 4d, the two kidneys shown are from littermates to illustrate the kidney size in agreement with the cumulative data shown in Figure 4e. Unfortunately, this litter did not have a wildtype control. As the data analysis in Figure 4e is based on littermates, mixing and matching kidneys of different litters does not seem appropriate. Thus, we have omitted showing a wildtype control in this panel. However, the size of the wildtype kidney can be seen in Figure 4a.

We have added the scale bar to both panels and have updated the figure legend to emphasize that the kidneys shown are from littermates and that no wildtype littermate was present in this litter.

(5) "Surprisingly, an 8-fold stronger interaction was observed between full-length PC1 and myc-mBicc1-ΔKH compared to mycmBicc1 or myc-mBicc1-ΔSAM." Assuming all the controls for protein folding and expression levels have been carried out and not shown/mentioned, this sentence seems to contradict the previous statement that Bicc1deltaSAM reduced the interaction with PC1 by 55%. Because the full length and SAM deletion have different interaction strengths, the latter sentence makes no sense.

The reduction in the levels of myc-mBicc1-ΔSAM compared to wildtype mycmBicc1 in respect to PC1 binding was not significant. We have clarified this in the text.

We have corrected the sentence and modified the Figure accordingly. 

(6) Imprecise statements make a reader wonder how to interpret the data: "More than three independent experiments were analyzed." Stating the sample size or including it in the figure would save space and improve confidence in the data presented.

We have stated the exact number of animals per conditions above each of the bars.

(7) "Next, we performed a similar mouse study for Pkd1 by reducing the gene dose of Pkd1 postnatally in the collecting ducts using a Pkhd1-Cre as previously described40" What did the authors mean?

The reference was included to cite the mouse strain, but realized that it can be mis-interpreted that the exact experiments has been performed previously. We have clarified this in the text.

We have reworded the sentence to avoid misinterpretation. 

(8) The authors examined the additive effects of knocking down Bicc1, Pkd1, and Pkd2 with morpholinos in Xenopus and, genetically, in mice. While the Bicc1[+/-] Pkd1 or 2[+/-] double heterozygote mice did not show phenotypes, the authors report that the Bicc1[-/-] Pkd1 or 2 [+/-] did instead show enlarged kidneys. What is the phenotype of a Bicc1[+/-] Pkd1 or 2 [-/-]? What we learn from the author's findings among the PKD population suggests that the latter situation would be potentially translationally relevant.

The mouse experiments were designed to address a cooperativity between Bicc1 and either Pkd1 or Pkd2 and whether removal of one copy of Pkd1 or Pkd2 would further worsen the Bicc1 cystic kidney phenotype. Thus, the parental crosses were chosen to maximize the number of animals obtained for these genotypes. Unfortunately, these crosses did not yield the genotypes requested by the reviewer. To address the contribution of Bicc1 towards the PKD population, we will need to perform a different cross, where we eliminate Pkd1 or Pkd2 in a floxed background of Bicc1 postnatally in adult mice. While we are gearing up to perform such an experiment, this is timewise beyond the scope of the manuscript. In addition, please note that we have addressed the question about the translation towards the PKD population already in the discussion of the original submission (page 13/14, last/first paragraph).

No changes have been made to the revised version of the manuscript.

(9) How do the authors interpret the milder effects of the Bicc1[-/-] Pkd1[+/-] compared to Bicc1[-/-] Pkd2[+/-] relative to the respective protein-protein interactions?

The milder effects are due to the nature of the crosses. While the Pkd2 mutant is a germline mutation, the Pkd1 mutant is a conditional allele eliminating Pkd1 only in the collecting ducts of the kidney. As such, we spare other nephron segments such as the proximal tubules, which also significantly contribute to the cyst load. As such these mouse data support the interaction between Pkd1 and Pkd2 with Bicc1, but do not allow us to directly compare the outcomes. While this was mentioned in the previous version of the manuscript, we have expanded on this in the revised version of the manuscript.

We have expanded the results section in the revised version of the manuscript highlighting that the two different approaches cannot be directly compared.

(10) How do the authors interpret that the strong Bicc1[Bpk] Pkd1 or Pkd2 double heterozygote mice did not have defects and "kidneys from Bicc1+/-:Pkd2+/- did not exhibit cysts (data not shown)", when the VEO PKD patients and - although not a genetic reduction - also the morpholino-treated Xenopus did?

VEO PKD patients are characterized by a loss of function of PKD1 or PKD2 and – as we propose in this manuscript - that BICC1 further aggravates the phenotype. Yet, we do not address either in the mouse or Xenopus experiments whether BICC1 is a genetic modifier. We are simply addressing whether the two genes show a genetic interaction. In the mouse studies, we eliminate one copy of Pkd1 or Pkd2 in the background of a hypomorphic allele of Bicc1. Similarly, in the Xenopus experiments, we employ suboptimal doses of the morpholino oligomers, i.e., concentrations that did not yield a phenotypic change and then asked whether removing both together show cooperativity. It is important to state that this is based on a biological readout and not defined based on the amount of protein. While we have described this already in the original manuscript (page 7, first paragraph), we have amended our description of the Xenopus experiment to make this even clearer. 

Finally, we agree with the reviewer that if we were to address whether Bicc1 is a modifier of the PKD phenotype in mouse, we would need to reduce Bicc1 function in a Pkd1 or Pkd2 mutants. Yet, we have recognized this already in the initial version of the manuscript in the discussion (page 14, first paragraph).

We have expanded the results section when discussing the suboptimal amounts of the morpholino oligos (Page 6, 1^st paragraph).

(11) Unclear: "While variants in BICC1 are very rare, we could identify two patients with BICC1 variants harboring an additional PKD2 or PKD1 variant in trans, respectively." Shortly after, the authors state in apparent contradiction that "the patients had no other variants in any of other PKD genes or genes which phenocopy PKD including PKD1, PKD2, PKHD1, HNF1s, GANAB, IFT140, DZIP1L, CYS1, DNAJB11, ALG5, ALG8, ALG9, LRP5, NEK8, OFD1, or PMM2."

The reviewer is correct. This should have been phrased differently. We have now added “Besides the variants reported below” to clarify this more adequately.

The sentence was changed to start with “Besides the variants reported below, […].”

(12) "The demonstrated interaction of BICC1, PC1, and PC2 now provides a molecular mechanism that can explain some of the phenotypic variability in these families." How do the authors reconcile this statement with their reported ultra-rare occurrence of the BICC1 mutations?

As mentioned in the manuscript and also in response to the other two reviewers, Bicc1 has been shown to regulate Pkd2 gene expression in mice and frogs via an interaction with the miR-17 family of microRNAs. Moreover, the miR-17 family has been demonstrated to be critical in PKD (PMID: 30760828, PMID: 35965273, PMID: 31515477, PMID: 30760828). In fact, both other reviewers have pointed out that we should stress this more since Bicc1 is part of this regulatory pathway. Future experiments are needed to address whether Bicc1 contributes to the variability in ADPKD onset/severity. Yet, this is beyond the scope of this study. 

Based on the comments of the two other reviewers we have further addressed the Bicc1/miR-17 interaction.

(13) The manuscript should use correct genetic conventions of italicization and capitalization. This is an issue affecting the entire manuscript. Some exemplary instances are listed below.

(a) "We also demonstrate that Pkd1 and Pkd2 modifies the cystic phenotype in Bicc1 mice in a dose-dependent manner and that Bicc1 functionally interacts with Pkd1, Pkd2 and Pkhd1 in the pronephros of Xenopus embryos." Genes? Proteins?

The data presented in this section show that a hypomorphic allele of Bicc1 in mouse and a knockdown in Xenopus yields this. As both affect the proteins, the spelling should reflect the proteins.

No changes have been made in the revised manuscript.

(b) The sentence seems to use both the human and mouse genetic capitalization, although it refers to experiments in the mouse system “to define the Bicc1 interacting domains for PC2 (Fig. 2d,e). Full-length PC2 (PC2-HA) interacted with full-length myc-mBICC1.”

We agree with the review that stating the species of the molecules used is critical, we have adapted a spelling of Bicc1, where BICC1 is the human homologue, mBicc1 is the mouse homologue and xBicc1 the Xenopus one.

We have highlighted the species spelling in the methods section and labeled the species accordingly throughout the manuscript and figures. 

(14) “Together these data supported our biochemical interaction data and demonstrated that BICC1 cooperated with PKD1 and PKD2.” Are the authors implying that these results in mice will translate to the human protein?

We agree that we have not formally shown that the same applies to the human proteins. Thus, we have changed the spelling accordingly.

We have revised the capitalization of the proteins. 

(15) The text is often unclear, terse, or inconsistent.

(a) “These results suggested that the interaction between PC1 and Bicc1 involves the SAM but not the KH/KHL domains (or the first 132 amino acids of Bicc1). It also suggests that the N-terminus could have an inhibitory effect on PC1-BICC1 association.” How do the authors define the N-terminus? The first 132 aa? KH/KHL domains?

This was illustrated in the original Figure 2A. The DKH constructs lack the first 351 amino acids. 

To make this more evident, we have specified this in the text as well.

(b) Similarly, the authors state below, "Unlike PC1, PC2 interacted with mycmBICC1ΔSAM, but not myc-mBICC1-ΔKH suggesting that PC2 binding is dependent on the N-terminal domains but not the SAM domain." It is unclear if the authors refer to the KH/KHL domains or others. Whatever the reference to the N-terminal region, it should also be consistent with the section above.

This is now specified in the text.

(c) Unclear: "We have previously demonstrated that Pkd2 levels are reduced in a complete Bicc1 null mice,22 performing qRT-PCR of P4 kidneys (i.e. before the onset of a strong cystic phenotype), revealed that Bicc1, Pkd1 and Pkd2 were statistically significantly down9 regulated (Fig. 4h-j)".

We have changed the text to clarify this. 

(d) “Utilizing recombinant GST domains of PC1 and PC2, we demonstrated that BICC1 binds to both proteins in GST-pulldown assays (Fig. 1a, b)." GST-tagged domains? Fusions?

We have changed the text to clarify this. 

(e) "To study the interaction between BICC1, PKD1 and PKD2 we combined biochemical approaches, knockout studies in mice and Xenopus, genetic engineered human kidney cells" > genetically engineered.

We have changed the text to clarify this.

(f) Capitalization (e.g., see Figure S3, ref. the Bpk allele) and annotation (e.g., Gly821Glu and G821E) are inconsistent.

We have homogenized the labeling of the capitalization and annotations throughout the manuscript. 

(g) What do the authors mean by "homozygous evolutionarily well-conserved missense variant"?

We have changed this is the revised version of the manuscript. 

Reviewer #3 (Public review/Recommendations to the authors):

(1) A further study in HUREC cells investigating the critical regulatory role of BICC1 and potential interaction with mir-17 may yet lead to a modifiable therapeutic target.

(2) This study should ideally include experiments in HUREC material obtained from patients/families with BICC1 mutations and studying its effects on the PKD1/2 complex in primary cell lines.

This is an excellent suggestion. We agree with the reviewer that it would have been interesting to analyze HUREC material from the affected patients. Unfortunately, besides DNA and the phenotypic analysis described in the manuscript neither human tissue nor primary patient-derived cells collected once the two patients with the BICC1 p.Ser240Pro variant passed away.

No changes to the revised manuscript have been made to address this point.

(3) Please remove repeated words in the following sentence in paragraph 2 of the introduction: "BICC1 encodes an evolutionarily conserved protein that is characterized by 3 K-homology (KH) and 2 KH-like (KHL) RNA-binding domains at the N-terminus and a SAM domain at the C-terminus, which are separated by a by a disordered intervening sequence (IVS).23-28".

This has been changed.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

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

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

We thank the reviewer for acknowledging the strengths of our study.

Weaknesses and Limitations:

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

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

We acknowledge the value of dynamic measurements and clarify our methodological rationale.

While luliani et al. provided valuable temporal resolution through protein dynamics, our mRNA FISH approach achieves direct decoupling of transcriptional vs. post-translational regulation (Fig 4F-H), and condition flexibility across 7 growth rates (30-66 min doubling times). This trade-off sacrifices temporal resolution for enhanced population-scale resolution and perturbation flexibility. To directly address temporal coupling, future work will implement dual-color live imaging of DnaA activity concurrent with replication initiation events.

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

We agree that model transparency is essential for quantitative validation. To address this, all model parameters (DnaA synthesis rate, activation/deactivation rates etc.) are explicitly tabulated in Supplementary Information Table S6. For the titration (Hansen et al. 1991) and extrusion models, we derive analytical expressions for initiation mass (IM) sensitivity to DnaA expression in Supplementary Note 1. For Figure 2G/S6, we used published parameters (Berger & Wolde 2022 SI Table 2) with experiment growth conditions (μ = 1.54 h^-1).

The extrusion model's validation relies primarily on its ability to resolve paradoxical initiation events under dnaA shutdown (Fig 6C), a test where other models fail categorically. While the Berger titration-switch hybrid can fit steady-state IM trends (Fig S6A), it cannot reproduce post-shutdown dynamics without ad hoc modifications (Fig S6B). We acknowledge that comprehensive analysis of all model regimes exceeds this study's scope but provide full simulation code for independent verification: https://github.com/BaiYangBqdq/dynamics_of_biomass_DNA_coordination

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

We acknowledge the limitations of population-level inference and have refined our claims: "Replication initiation volume scales proportionally with peak DnaA activity volume with a slope of 1.0 (R₂=0.98, Fig 7G), indicating predictive correspondence rather than absolute coincidence. While population-level  𝑉_𝑖 estimation cannot resolve single-cell stochasticity, the consistent 𝑉*: 𝑉_𝑖 relationship across 20 conditions suggest DnaA activity thresholds predict initiation timing within physiological error margins”. Future work will implement simultaneously DnaA activity and replication forks by using microfluidic single-cell tracking.

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

We acknowledge the observed temporal deviations between DnaA activity peaks (𝑉*) and population-derived volumes at initiation ( 𝑉_𝑖) in certain conditions, in line with the findings of Iuliani et al. This might be mechanistically consistent with the time required for orisome assembly or oriC sequestration. They do not contradict our core finding that initiation occurs at a defined DnaA activity threshold (slope=1.0, R₂=0.98 in 𝑉*: 𝑉_𝑖 correlation).

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

We employed a plasmid-based reporter system to circumvent the significant confounding effects of chromosomal position on promoter activity, as extensively documented by Pountain et al., where local genomic context (e.g., nucleoid occlusion, supercoiling gradients, and neighboring operons) introduces uncontrolled variability. By housing the P_syn66 test promoter and P_con normalization control in identical low-copy pSC101 vectors (<8 copies/ cell, Peterson & Phillips, Plasmid 2008), we ensured they experience equivalent physical and biochemical environments. This ratiometric design, where DnaA activity is calculated, actively corrects for global fluctuations in RNA polymerase availability, nucleotide pools, and plasmid copy number. Critically, P_syn66’s architecture emulates natural DnaA-responsive elements: its strong DnaAboxes report free DnaA concentration, while its weak box is preferentially bound by DnaA-ATP (Speck et al., EMBO journal 1999), mirroring the nucleotide-state sensitivity of oriC and the native dnaA promoter. This system was indispensable for our central finding, as it uniquely enabled the decoupling of DnaA activity oscillations from transcriptional feedback (Fig. 4F-H), an experiment fundamentally impossible with chromosomally integrated reporters due to autoregulatory interference.

Overall Appraisal:

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

We thank the reviewer for highlighting the need for precise language in framing our conclusions. We have implemented the following substantive revisions throughout the manuscript to ensure claims align strictly with empirical evidence:

(1) Changed "redefine the paradigm for replication control" into "advance the paradigm for replication control" (Introduction)

(2) Changed "redefine bacterial cell cycle control" into "refine bacterial cell cycle control as a dynamic interplay..." (Discussion)

(3) Removed the term "spatial" from the Discussion's description of DnaA-chromosome interactions (Discussion, first paragraph).

(4) Changed "provides a blueprint" into "provides a valuable tool for dissecting spatial regulation..." (Discussion, final paragraph)

(5) Scrutinized all superlatives (e.g., "critical feat" into "important capability"; "fundamental principle of cellular organization" into "potential organizational strategy")

(6) Replaced the instances of "robust" with evidence-backed descriptors (e.g., "sensitive," "consistent")

(7) We agree that the extrusion model requires further validation and have emphasized this in Discussion: "While H-NS perturbation supports extrusion mechanism, future work should identify the full extruder interactome and elucidate how metabolic signals modulate their activity" (final paragraph)

This calibrated language more accurately represents our study as a conceptual advance with testable mechanisms, not a complete paradigm shift.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

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

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

We thank the reviewer for acknowledging the strengths of our study.

Weaknesses:

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

We thank the reviewer for this important observation. Our data demonstrate that increased dnaA mRNA levels induce two compensatory changes in cell cycle progression:

(1) Earlier replication initiation, manifested as a reduced initiation mass: the initiation mass decreased from 5.6 to 2.6 (OD₆₀₀·ml per 10¹⁰ cells) as the relative dnaA mRNA level increased from 0.2 to 7.2 (normalized to the wild-type level) (Fig. 2F, red).

(2) Prolonged C+D period: Increased by approximately 60% (from 1.05 to 1.66 hours, Fig. 2F blue).

The complete quantitative relationship is now explicitly described in the Results section: “Concurrently, the initiation mass was reduced by 50%, and the period from initiation to division (C+D) was increased by ~60% (Fig. 2F)”

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

The relative dnaA mRNA level was obtained by normalizing to that in wild-type MG1655 cells grown in the same medium. To clarify this point, we have now marked the wild-type level in Fig. 1B, and a clear description of this has also been included in the figure caption.

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

Thank you for your valuable suggestion. Increased dnaA mRNA accelerates DnaA accumulation, causing cells to reach the initiation threshold at a smaller cell size (reducing initiation mass, Fig. 2F red). This earlier initiation increases oriC copies per cell at populational level (Fig. 2E). This mechanistic interpretation now appears in the Results: “As the DnaA expression level increases, DnaA activity reaches the initiation threshold earlier. Given that cell mass remained nearly unchanged, this earlier initiation led to an increase in population-averaged cellular oriC numbers (Fig. 2E).”

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

All models presented in this article omit explicit modeling of dnaA mRNA dynamics for simplicity. However, at steady state, the relative level of dnaA mRNA can be approximated by the relative expression rate of DnaA protein, as both reflect the expression level of DnaA. This detail is now clarified in the caption of Figure 2G.

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

Schaechter's law describes the exponential scaling of average cell size with growth rate in bacteria. In our prior work (Zheng et al., Nature Microbiology 2020), where we demonstrated that Schaechter's law fails in slow-growth regimes. However, in current study, growth rate remained constant across different dnaA expression levels (Fig. 2C), and cell mass showed no significant change (Fig. 2D). Since Schaechter's law specifically addresses how cell size scales with growth rate, it does not apply here, as growth rate was invariant in our perturbations, which selectively alter replication initiation dynamics, not growth rate or size scaling.

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

The governing equations linking initiation mass and DnaA expression level is now provided in Supplementary Note S1 for both the titration and the extrusion model. In general, the dependence of initiation mass (𝑉_𝐼) on dnaA expression level (𝛼_𝐴) dependency takes an inverse 1 proportionality form: . In the extrusion model, the incorporated extruder protein is assumed to have similar synthesis dynamics as DnaA and can release DnaA from DnaA-box. After denoting the synthesis rate of the extruder as 𝛼_𝐻, the combined effect of DnaA and the extruder on replication initiation can be briefly described as: . Then the additive contribution of 𝛼_𝐻 dampens the sensitivity of initiation mass to changes in 𝛼_𝐴, resulting in a significantly flattened curve. As a result, the predicted 𝑉_𝐼 − 𝛼_𝐴 relationship has a concave shape in the semi-log plots.

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

Yes, the extrusion model can provide the initiation-to-initiation adder phenomenon, this information was provided in fig. S3C.

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

We acknowledge the reviewer's valid concern regarding the indirect nature of our DnaA activity measurements. While mRNA levels alone cannot resolve active DnaA dynamics, our approach integrates functional replication outcomes with a validated synthetic reporter to infer activity. Crucially, elevated dnaA mRNA causes demonstrable biological effects: earlier replication initiation (Fig. 2F) and increased oriC copies (Fig. 2E), directly confirming enhanced functional DnaA activity at the oriC locus. The P_syn66 reporter, engineered with DnaA-boxes mirroring oriC's architecture, provides orthogonal validation, showing progressive repression to dnaA induction (Fig. 3C). Our operational metric , bases on P_syn66 responds sensitively to DnaA-chromosome interactions within its characterized 8-fold dynamic range (Fig. 3C). Immunoblots would be inadequate here, as they cannot distinguish functionally critical pools: free versus chromosome-bound DnaA, or DnaA-ATP versus DnaAADP, precisely the post-translational states our study implicates in regulation. We therefore prioritize functional readouts (initiation timing) and the P_syn66 reporter, which probes the biologically active fraction relevant to replication control.

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

We acknowledge the reviewer's valid methodological concern and clarify that while bulk measurements carry inherent limitations, our approach is grounded in established techniques with demonstrated reliability. Cell mass was inferred from OD600/cell, which correlates strongly with direct dry weight measurements and microscopic cell volumes across diverse growth conditions, as validated in our prior work (Zheng et al., Nature Microbiology 2020). Crucially, cell mass remained invariant across dnaA expression levels (Fig. 2D).

Regarding oriC quantification, the rifampicin-cephalexin run-out assay is a wildly applied for replication initiation studies. Our data shows expected 2ⁿ oriC distributions without abnormal ploidy (as shown below). While single-cell methods offer superior resolution, our bulk approach provides accurate population-level trends.

Author response image 1.

Recommendations for the authors:

Reviewing Editor Comments:

The reviewers felt that the mathematical modeling was not adequately explained in the paper, and that this affected the readability of the manuscript. The authors are encouraged to elaborate on this aspect of the paper (in addition to strengthening other claims, if possible, per the reviewers' comments).

We thank the editor and reviewers for their constructive feedback. We have comprehensively strengthened the mathematical modeling framework to enhance clarity and rigor.

Reviewer #1 (Recommendations for the authors):

The only revision I would do is a recalibration of the claims and a major effort to clarify the modeling part (including a detailed SI appendix), without necessarily performing additional work.

To enhance mathematical modeling transparency, we have completed model description in the method section and a parameter table with literature-sourced values in Supplementary Information Table S6. Moreover, analytical derivations of initiation mass dependencies are performed and presented in the Supplementary Information Note S1.

Of course, there are extra experiments (mentioned in the public review) that would help support some of the big claims, but that can be considered a different project.

Thank you for your suggestion. This will be addressed in our future work.

Minor suggestion: please put signposts or plot jointly to compare the maxima/minima in Figures 4D, E, G, and H.

We added dashed lines in Figures 4D, and E, to synchronize visualization of DnaA activity peaks and transcriptional minima across panels, facilitating direct biological comparisons.

Reviewer #2 (Recommendations for the authors):

(1) Should define what DNA activity is.

We have explicitly defined DnaA activity in the Introduction as “the capacity to initiate replication…” and noted that it is “governed by free DnaA concentration, DnaA-ATP/-ADP ratio, and orisome assembly competence”.

(2) Word repetition - “...grown in in Luria-Bertani (LB) medium...”.

Corrected.

(3) Typographical error - “FISH ... was preformed" should be "performed”.

Corrected.

(4) The manuscript alternates between “ng ml^-1” and “ng·ml^-1”; choose one style and apply it uniformly.

Standardized the units to ng·ml^-1 throughout.

(5) Reference duplicates - Some citations appear twice in the bibliography (e.g., "Bintu et al., 2005a/b" and "Bintu et al., 2005b" listed again later).

The studies by Bintu et al. (2005a, 2005b) represent separate works: 2005a details applications, and 2005b develops models.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Reply to the Reviewers

We thank the reviewers for their positive assessments overall and for many helpful suggestions for clarification to make the manuscript more accessible to a broader audience. We made minor text changes and added more labels to the figures to address these comments.

• *

__Referee #1

__

Summary: In this study, the authors show a genetic interaction of the lipid receptors Lpr-1, Lpr-3 and Scav-2 in C. elegans. They show that Lpr-1 loss-of-function specifically affects aECM localization of Lpr-3 and attribute the lethality of Lpr-1 mutants to this phenotype. The authors performed a mutagenesis screen and identified a third lipid receptor, Scav-2, as a modulating factor: loss of scav-2 partially rescues the Lpr-1 phenotype. The authors created a variety of tools for this study, notably Crispr-Cas9-mediated knock-ins for endogenous tagging of the receptors.

Major comments:

1. while the authors provide a nice diagram showing the potential roles and interplay of lpr-1, lpr-3 and scav-2, it remains unclear what their respective cargo is. The nature of interaction between the proteins remains unclear from the data.

Response

• We agree that identifying the relevant cargo(s) will be key to understanding the detailed mechanisms involved and that the lack of such information is a limitation of our study. However, the impact of our study is to show that these lipid transporters functionally interact to affect aECM organization, a role that could be relevant to many systems, including humans.

As an optional (since time-consuming) experiment I would suggest trying more tissue-specific lipidomics.

Response

• This would be an interesting future experiment but is outside our current technical capabilities.

The lipidomics data should be presented in the figures, even if there were no significant changes. Importantly, show the lipid abundance at least of total lipids, better of individual classes, normalized to the material input (e.g. number of embryos, protein).

Response

• The reviewer is right to point out that lipid variations could occur at different levels, and that we should exercise caution. However, the unsupervised lipidomics analysis would have detected not only individual lipid variations, but also variations in the total or subgroup lipid content. Indeed, the eggs were weighed prior to extraction and each sample was extracted with the same precise volume of solvent before analysis. Furthermore, the LC-MS/MS injection sequence included blanks and quality control (QC) samples. The blanks were the extraction solvent, which allowed us to control for features unrelated to the biological samples. The QC sample was a mixture of all the samples included in the injection sequence, reflecting the central values of the model. If a subclass of samples, such as the lpr-1 mutant, had been characterized by a decrease in one lipid, a subgroup of lipids, or all lipids, it would have clustered separately. Instead, our PCA showed that the variation between samples of the same genotype (wild type, lpr-1 mutant, or lpr-1; scav-2) was similar to the variation between samples from two different genotypes. This means that we did not detect modifications to lipid quantity specifically or in total. A figure illustrating the lipid contents would show no difference between groups.

Figure 1g: I do not understand what the lpr3:gfp signal is: the punctae in the overview image? and where are they in the zoom image showing anulli and alae? Also, how where the anulli and alae structures labeled? please provide more information

Response

• All of the fluorescent signal shown in this figure panel corresponds to the indicated LPR fusion - no other labelling method was used. SfGFP::LPR-3 labels the matrix structures (alae and annuli) as well as some puncta – the ratio of matrix to puncta changes over developmental stages. We edited the figure legend to make this more clear.

One point that is not sufficiently adressed is that the authors deduce from the inability of the scav-2 gfp knock in to suppress lpr1 lethality that scav2 function is not impaired. This is quite indirect. Can the authors provide more convincing evidence that scav-2 ki has normal function?

Response

• Suppression of lpr-1 (or other aECM mutant) lethality is the only known phenotype caused by loss of scav-2 Therefore, this is the only phenotype for which we can do a rescue experiment to test functionality of the knock-in. The data presented do indicate that the knock-in fusion retains significant function.

In general, the data is clearly presented and the statistical analyses look sound.

Response

• Thank you

__Minor comments: __

Please provide page and line numbers!

Response:

• done

Avoid contractions like "don't" in both text and figure legends

Response:

• changed one instance of “don’t” to “do not”

Page 12: I do not understand the meaning of the sentence "This transgene also caused more modest lethality in a wild-type background"

Response:

• Wording changed to “This transgene caused very little lethality in a wild-type background (Fig. 6C), indicating it is not generally toxic.”

Figure 7: what is meant with "Dodt"?

Response:

• Dodt gradient contrast imaging is a method for transmitted light imaging similar to DIC and is used on some confocal microscopes. It is now explained in the Methods section. We removed the Dodt label from Figure 7 since it seems to be confusing and it is not really important whether the brightfield image is DIC or Dodt.

  Reviewer #1 (Significance (Required)):

  The study is experimentally sound and uses numerous novel tools, such as endogenously tagged lipid receptors. It is an interesting study for researchers in basic research studying lipid receptors and ECM biology. It provides insights on the genetic interaction of lipid receptors. My expertise is in lipid biochemistry, inter-organ lipid trafficking and imaging. I am not very familiar with C. elegans genetics.

__Referee #2 __ 1. The manuscript is very well written; the documentation is fine, but some more details are needed for better following the subject for readers not familiar with nematode anatomy.

For instance, while alae are somehow explained, annuli are not - structures that look abnormal in lpr1 and lpr1-scav2 mutants (Fig. 5B).

Response

• Apologies for this oversight. We added annuli labels to Figure 1 and Figure 5 panels and added descriptions of annuli to the Figure 1 legend and the Results text.

Moreover, the authors show in Fig. 1 the punctae etc in the epidermis, whereas in Fig. 2 the show Lpr3 accumulation or not in the duct and the pore (lpr1). How do they localize in the cells of these structures at high magnification? It is also important to see the Lpr3 localisation in lpr1 mutants shown in Fig. 2A with the quality of the images shown in Fig. 1F. This applies also to Figs. 4 and 5.

Responses:

• The embryonic duct and pore cells are very small and we have not reliably seen puncta within them. In Figs 2 and 5, we supplemented the duct and pore images with those from the epidermis, which is a much larger tissue, allowing us to resolve puncta and matrix structures with better resolution.
• The laser settings in Figs 2,4,5 (as opposed to Fig. 1) were chosen to avoid saturation of the matrix signal so that we could do accurate quantifications as shown. The images are unmodified with respect to brightness and therefore appear relatively dim – but we think they convey the observations very accurately.

I would like to see punctae in lpr1-scav2 doubles.

Response:

• Puncta in this genotype are shown for the epidermis in Figure 5. It has not been possible to see puncta specifically within the embryonic duct and pore.

Regarding the central mechanism, one possibility is - what the authors describe - that Lpr1 is needed for Lpr3 accumulation in ducts and tubes. Alternatively, Lpr1 is needed for duct and tube expansion, in lack of which Lpr3 is unable to reach its destination that is the lumina. Scav2, in this scenario, might be antagonist of tube and duct expansion, and thereby rescue the Lpr1 mutant phenotype independently. Admittedly, the non-accumulation of Lpr3 in scav2 mutants argues against a lpr1-independent function of scav2.

Responses:

• LPR-1 is indeed needed to maintain duct and pore tube integrity as the tubes grow, but in mutants the tubes appear to collapse at a later stage than we imaged here (Stone et al 2009). The ~normal accumulation of LET-4 and LET-653 further argues that the duct and pore tubes are still intact at the 1.5-to-2-fold stages. Therefore, we conclude that the defect in LPR-3 accumulation precedes duct and pore collapse.
• The changes we document in the epidermis also show that the lpr-1 mutant affects LPR-3 accumulation in another (non-tube) tissue.

In any case, to underline the aspect of Lpr1-Scav2 dosage relationship, the authors may also have a look at Lpr3 distribution in lpr1 heterozygous, and lpr1-scav2 double heterozygous worms. In this spirit, it would be interesting to see the semi-dominant effects of scav2 on Lpr3 localisation in lpr1 mutants by microscopy.

Response:

• Because of the hermaphroditism of C. elegans, it would be technically challenging to confidently identify heterozygous (vs. homozygous) embryos for confocal imaging. We do not think that the results would be informative enough to warrant the effort, given that we’ve already shown that scav-2 heterozygosity can partly suppress lpr-1 The expectation is that LPR-3 levels would be partially restored in the scav-2 het, but it might take a very large sample size to confidently assess that partial effect.

One word to the overexpression studies: it is surprising that the amounts of Scav2 delivered by the expression through the grl-2 promoter in the lpr1, scav2 background are almost matching those by the opposite effect of scav2 mutations on lpr1 dysfunction.

Response:

• The reviewer refers to the transgenic rescue experiment with the grl-2pro::SCAV-2 transgene. Because the scav-2 mutant phenotype being tested is suppression of lpr-1 lethality, the expected result from scav-2 rescue is to restore the lpr-1 lethal phenotype to the strain. This is exactly the result we see. We have revised the text to more clearly explain the logic.

One issue concerns the localization of scav2-gfp "rarely" in vesicles: what are these vesicles?

Response

• Only a handful of vesicles were seen across all the images we collected, and we have not yet identified them. They could be associated with either SCAV-2 delivery or removal from the plasma membrane, as now stated in the text. SCAV-2 trafficking would be an interesting area for further study but is beyond the scope of this paper.

One comment to the Let653 transgenes/knock-ins: the localization of transgenic Let653-gfp may be normal in lpr1 mutants because there are wild-type copies in the background.

Response

• There are wild type copies of LET-653 in the background, but no wild type copies of LPR-1. Even if the untagged LET-653 would be recruiting the tagged LET-653 as the reviewer suggests, we can still conclude that lpr-1 loss does not prevent the untagged LET-653 (and thus also the tagged LET-653) from accumulating in the duct lumen matrix.

One thought to the model: if Scav2 has a function in a lpr1 background, this means that yet another transporter X delivers the substrate for Scav2, isn't it?

Response

• Yes, we completely agree with this interpretation and have revised the discussion and Figure 8 legend to more explicitly make this point.

A word to the term haploinsifficient that is used in this study: scav2 mutants would be haploinsifficient if the heterozygous worms died in an otherwise wild-type background.

Response

• We disagree with this comment. The term “haploinsufficient” simply means that heterozygosity for a deletion or other loss of function allele can cause a mutant phenotype – the term is not restricted to lethal phenotypes.

  Reviewer #2 (Significance (Required)):

  Alexandra C.Belfi and colleagues wrote the manuscript entitled "Opposing roles for lipocalins and a CD36 family scavenger receptor in apical extracellular matrix-dependent protection of narrow tube integrity" in which they report on their findings on the genetic and cell-biological interaction between the lipid transporters Lpr1 and scav2 in the nematode C. elegans. In principle, these two proteins are involved in shaping the apical extracellular matrix (aECM) of ducts by regulating the amounts of Lpr3 in the extracellular space. While seems to act cell autonomously, Lpr1 has a non-cell autonomous effect on Lpr3.

---

__Referee #3 __ Summary: Using a powerful combination of genetic and quantitative imaging approaches, Belfi et al., describe novel findings on the roles of several lipocalins-secreted lipid carrier proteins-in the production and organization of the apical extracellular matrix (aECM) required for small diameter tube formation in C. elegans. The work comprises a substantial extension of previous studies carried out by the Sundaram lab, which has pioneered studies into the roles of aECM and accessory proteins in creating the duct-pore excretion tube and which also plays a role in patterning of the epidermal cuticle. One core finding is that the lipocalin LPR-1 does not stably associate with the aECM but is instead required for the incorporation of another lipocalin, LPR-3. A second major finding is that reduction of function in SCAV-2, a SCARB family membrane lipid transporter, suppresses lpr-1 mutant lethality along with associated duct-pore defects and mislocalization of LPR-3. Likewise loss of scav-2 partially suppresses defects in two other aECM proteins and restores defects in LPR-3 localization in one of them (let-653). Additional genetic and protein localization studies lead to the model that LPR-1 and SCAV-2 may antagonistically regulate one or more lipid or lipoprotein factors necessary for LPR-3 localization and duct-pore formation. A role for LPR-1 and LPR-3 at lysosomes is clearly implicated based on co-localization studies, although a specific role for lysosomes (or related organelles) is not defined. Finally, MS data suggests that neither LPR-1 or SCAV-2 grossly affect lipid composition in embryos, consistent with dietary interventions failing to affect mutant phenotypes. Ultimately, a plausible schematic model is presented to explain for much of the data.

__*Major comments:

*__

1. The studies are very thorough, convincing, and generally well described. Conclusions are logical and well grounded. Additional experiments are not required to support the authors major conclusions, and the data and methods are described in a sufficient detail to allow replication. As such my comments are minor and should be addressable at the author's discretion in writing.

Response

• Thank you for these positive comments

  __Minor comments: __2) In the abstract, "tissue-specific suppression" made me think that there was going to be a tissue-specific knockdown experiment, which was not the case. Rather scav-2 suppression is specific to the duct-pore, which corresponds to where scav-2 is expressed. Consider rewording this.

Response

• Wording was changed to “duct/pore-specific suppression”

  3) Page 5. Suggest wording change to, "Whereas LPR-3 incorporates stably into the precuticle, suggesting a structural role in matrix organization, LPR-1..."

Response

• Done

  4) LIMP-2 versus LIMP2. Both are used. Uniprot lists LIMP2, but some papers use LIMP-2. Choose one and be consistent.

Response

• Everything changed to LIMP2.

  5) Some of the data for S6 Fig wasn't referred to directly in the text. Namely results regarding pcyt-1 and pld-1. I'd suggest incorporating this into the results section possibly using, "As a control for our lipid supplementation experiments..."

Response

• These experiments are now described on page 11.

  6) Page 12 bottom. I understand the use of "oppose", but another way to put it is that SCAV-2 and LPR-1 (antagonistically or collectively) modulate aECM composition. Other terms that might confuse some readers is the use of upstream and downstream, although I OK with its use in the context of this work.

Response

• The genetics indicate that lpr-1 and scav-2 have opposite effects on tube shaping and LPR-3 localization, so they do function antagonistically rather than collectively/cooperatively; we decided to keep this terminology.

  7) Page 16. I understand the logic that SCAV-2 is unlikely to directly modulate LPR-3 given its presumed molecular function. But is it possible that LPR-3 levels are already maxed out in the aECM so that loss of SCAV-2 doesn't lead to any increase? Conversely, one could argue that even if acting indirectly, SCAV-2 could have led to increased LPR-3 levels, unless they were already maxed.

Response

• This is a good point and the possibility is now mentioned in the Results page 9. We also changed our wording in the Abstract and Discussion to acknowledge the possibility that LPR-3 could be the SCAV-2 cargo, though we still don’t favor this model.

  8) Figure legend 1. I did not see an asterisk in figure 1B.

Response

• thanks for catching this error, text removed

  9) Figure 1C. Might want to define the "degree" term in the legend for people outside the field.

Response

• We added an explanation to the figure legend.

  10) Fig 1 G. I was just wondering if cuticle autofluorescence was an issue for taking these images.

Response

• Cuticle auto fluorescence is generally quite dim in L4s with our settings, and it was not an issue at this mid/late L4 stage, which corresponds to when both LPR fusions are at their brightest. Note that both large panels are MAX projections and yet you can’t see any cuticle auto-fluorescence in the LPR-1 panel.

  11) Fig 2 and others. Please define error bars.

Response

• These correspond to the standard deviation; this information is now added to the Methods.

  12) Fig 5. From the images, it looks like lpr-1; scav-2 doubles might have a worse (pre)cuticle defect in LPR-3 localization than lpr-1 singles. If so that would be interesting and would suggest that their relationship with respect to the modulation of LPR-3 is context dependent. Admittedly, the lack of obvious scav-2 expression in the epidermis would not be consistent with an effect (positive or negative).

Response

• The lpr-1 scav-2 strain is certainly not improved over lpr-1 but we have not noted any consistent worsening of the phenotype either.

  13) Consider defining Dodt in the first figure legend where it appears.

Response

• Dodt gradient contrast imaging is a method of transmitted light imaging similar to DIC and is used on some confocal microscopes. It is now explained in the Methods section. We removed the term from Figure 7 since it seems to be confusing.

  14) For Mander's, is there a reason to report just one of the two findings (M1 or M2) versus both?

Response

• We now include the 2nd Manders value in the figure legend and note that value is much lower (0.25) because much of the red signal is lysosomes (where green would be quenched by acidity).

  15) Consider referring to specific panels (A, B...) within references to the supplemental files.

Response

• done

  16) Fig S6E. Neither "increasing nor increasing" to "increasing nor decreasing".

Response

• fixed

  **Referees cross-commenting**

  I thought that Reviewers 1 and 2 brought up some good points. My sense is that Belfi and colleagues can address most of these in writing, but are of course welcome to add new data as they see fit. I get that it's not a "perfect" paper where everything is explained fully or comes together, but I don't see that as a flaw that needs to be fixed. I think that the manuscript represents a good deal of work (as it is) and provides a sufficient advance while also suggesting an interesting link to disease. It will be up to individual journals to decide if the findings meets their criteria.

  Reviewer #3 (Significance (Required)):

  Significance: The work carried out in this paper, and more generally by the Sundaram lab, always has a ground-breaking element because very few labs in the field have studied in detail the developmental roles and regulation of the aECM, in large part because it can be challenging to dissect. The core findings in this study are rather novel and unexpected, namely the opposing roles of the paralogous LPR-1 and LPR-3 lipocalins and their functional interactions with SCAV-2. The study does stop short of finding specific molecules (lipid or lipoprotein) that would mediate the effects they report, and it wasn't yet clear how the lysosomal co-loc plays a role, but this is not a criticism of the work presented or the forward progress. I was particularly intrigued by the idea, presented in the discussion, that disruption of vascular aECM could potentially account for some of the (complex) observations regarding the role of lipocalins and SCARB proteins in human disease. This would represent a new avenue for researchers to consider and underscores the power of using non-biased approaches in model systems.

  As for all my reviews, this is signed by David Fay.

• *

Overall thoughts: This is an interesting history piece regarding peer review and the development of review over time. Given the author’s conflict of interest and association with the Centre developing MetaROR, I think that this paper might be a better fit for an information page or introduction to the journal and rationale for the creation of MetaROR, rather than being billed as an independent article. Alternatively, more thorough information about advantages to pre-publication review or more downsides/challenges to post-publication review might make the article seem less affiliated. I appreciate seeing the history and current efforts to change peer review, though I am not comfortable broadly encouraging use of these new approaches based on this article alone.

Page 3: It’s hard to get a feel for the timeline given the dates that are described. We have peer review becoming standard after WWII (after 1945), definitively established by the second half of the century, an example of obligatory peer review starting in 1976, and in crisis by the end of the 20th century. I would consider adding examples that better support this timeline – did it become more common in specific journals before 1976? Was the crisis by the end of the 20th century something that happened over time or something that was already intrinsic to the institution? It doesn’t seem like enough time to get established and then enter crisis, but more details/examples could help make the timeline clear. 

Consider discussing the benefits of the traditional model of peer review.

Table 1 – Most of these are self-explanatory to me as a reader, but not all. I don’t know what a registered report refers to, and it stands to reason that not all of these innovations are familiar to all readers. You do go through each of these sections, but that’s not clear when I initially look at the table. Consider having a more informative caption. Additionally, the left column is “Course of changes” here but “Directions” in text. I’d pick one and go with it for consistency.

3.2: Considering mentioning your conflict of interest here where MetaROR is mentioned.

With some of these methods, there’s the ability to also submit to a regular journal. Going to a regular journal presumably would instigate a whole new round of review, which may or may not contradict the previous round of post-publication review and would increase the length of time to publication by going through both types. If someone has a goal to publish in a journal, what benefit would they get by going through the post-publication review first, given this extra time?

There’s a section talking about institutional change (page 14). It mentions that openness requires three conditions – people taking responsibility for scientific communication, authors and reviewers, and infrastructure. I would consider adding some discussion of readers and evaluators. Readers have to be willing to accept these papers as reliable, trustworthy, and respectable to read and use the information in them. Evaluators such as tenure committees and potential employers would need to consider papers submitted through these approaches as evidence of scientific scholarship for the effort to be worthwhile for scientists.

Based on this overview, which seems somewhat skewed towards the merits of these methods (conflict of interest, limited perspective on downsides to new methods/upsides to old methods), I am not quite ready to accept this effort as equivalent of a regular journal and pre-publication peer review process. I look forward to learning more about the approach and seeing this review method in action and as it develops.

Response to the Editors and the Reviewers

I am sincerely grateful to the editors and peer reviewers at MetaROR for their detailed feedback and valuable comments and suggestions. I have addressed each point below.

Handling editor

1. “However, the article’s progression and arguments, along with what it seeks to contribute to the literature need refinement and clarification. The argument for PRC is under-developed due to a lack of clarity about what the article means by scientific communication. Clarity here might make the endorsement of PRC seem like less of a foregone conclusion.”

The structure of the paper (and discussion) has changed significantly to address the feedback.

2. “I strongly endorse the main theme of most of the reviews, which is that the progression and underlying justifications for this article’s arguments needs a great deal of work. In my view, this article’s main contribution seems to be the evaluation of the three peer review models against the functions of scientific communication. I say ‘seems to be’ because the article is not very clear on that and I hope you will consider clarifying what your manuscript seeks to add to the existing work in this field. In any case, if that assessment of the three models is your main contribution, that part is somewhat underdeveloped. Moreover, I never got the sense that there is clear agreement in the literature about what the tenets of scientific communication are. Note that scientific communication is a field in its own right.”

I have implemented a more rigorous approach to argumentation in response. “Scientific communication” was replaced by “scholarly communication.”

3. “I also agree that paper is too strongly worded at times, with limitations and assumptions in the analysis minimised or not stated. For example, all of the typologies and categories drawn could easily be reorganised and there is a high degree of subjectivity in this entire exercise. Subjective choices should be highlighted and made salient for the reader. Note that greater clarity, rigour, and humility may also help with any alleged or actual bias.”

I have incorporated the conceptual framework and description of the research methodology. However, the Discussion section reflects my personal perspective in some points, which I have explicitly highlighted to ensure clarity.

4. “I agree with Reviewer 3 that the ‘we’ perspective is distracting.”

This has been fixed.

5. “The paragraph starting with ‘Nevertheless’ on page 2 is very long.”

The text was restructured.

6. “There are many points where language could be shortened for readability, for example:

Page 3: ‘decision on publication’ could be ‘publication decision’.

Page 5: ‘efficiency of its utilization’ could be ‘its efficiency’.

Page 7: ‘It should be noted…’ could be ‘Note that…’.”

I have proofread the text.

7. “Page 7: ‘It should be noted that..’ – this needs a reference.”

This statement has been moved to the Discussion section, paraphrased, and reference added

“It should be also noted that peer review innovations pull in opposing directions, with some aiming to increase efficiency and reduce costs, while others aim to promote rigor and increase costs (Kaltenbrunner et al., 2022).”

8. “I’m not sure that registered reports reflect a hypothetico-deductive approach (page 6). For instance, systematic reviews (even non-quantitative ones) are often published as registered reports and Cochrane has required this even before the move towards registered reports in quantitative psychology.”

I have added this clarification.

9. “I agree that modular publishing sits uneasily as its own chapter.”

Modular publishing has been combined with registered reports into the deconstructed publication group of models, now Section 5.1.

10. “Page 14: ‘The "Publish-Review-Curate" model is universal that we expect to be the future of scientific publishing. The transition will not happen today or tomorrow, but in the next 5-10 years, the number of projects such as eLife, F1000Research, Peer Community in, or MetaROR will rapidly increase’. This seems overly strong (an example of my larger critique and that of the reviewers).”

This part of the text has been rewritten.

Reviewer 1

11. “For example, although Model 3 is less chance to insert bias to the readers, it also weakens the filtering function of the review system. Let’s just think about the dangers of machine-generated articles, paper-mills, p-hacked research reports and so on. Although the editors do some pre-screening for the submissions, in a world with only Model 3 peer review the literature could easily get loaded with even more ‘garbage’ than in a model where additional peers help the screening.”

I think that generated text is better detected by software tools. At the same time, I tried and described the pros and cons of different models in a more balanced way in the concluding section.

12. “Compared to registered reports other aspects can come to focus that Model 3 cannot cover. It’s the efficiency of researchers’ work. In the care of registered reports, Stage 1 review can still help researchers to modify or improve their research design or data collection method. Empirical work can be costly and time-consuming and post-publication review can only say that ‘you should have done it differently then it would make sense’.”

Thank you very much for this valuable contribution, I have added this statement at P. 11.

13. “Finally, the author puts openness as a strength of Model 3. In my eyes, openness is a separate question. All models can work very openly and transparently in the right circumstances. This dimension is not an inherent part of the models.”

I think that the model, providing peer reviews to all the submissions, ensures maximum transparency. However, I have made effort to make the wording more balanced and distinguish my personal perspective from the literature.

14. “In conclusion, I would not make verdict over the models, instead emphasize the different functions they can play in scientific communication.”

This idea has been reflected now in the concluding section.

15. “A minor comment: I found that a number of statements lack references in the Introduction. I would have found them useful for statements such as ‘There is a point of view that peer review is included in the implicit contract of the researcher.’”

Thank you for your feedback. I have implemented a more rigorous approach to argumentation in response.

Reviewer 2

16. “The primary weakness of this article is that it presents itself as an 'analysis' from which they 'conclude' certain results such as their typology, when this appears clearly to be an opinion piece. In my view, this results in a false claim of objectivity which detracts from what would

otherwise be an interesting and informative, albeit subjective, discussion, and thus fails to discuss the limitations of this approach.”

I have incorporated the conceptual framework and description of the research methodology. However, the Discussion section reflects my personal perspective in some points, which I have explicitly highlighted to ensure clarity.

17. “A secondary weakness is that the discussion is not well structured and there are some imprecisions of expression that have the potential to confuse, at least at first.”

The structure of the paper (and discussion) has changed significantly.

18. “The evidence and reasoning for claims made is patchy or absent. One instance of the former is the discussion of bias in peer review. There are a multitude of studies of such bias and indeed quite a few meta-analyses of these studies. A systematic search could have been done here but there is no attempt to discuss the totality of this literature. Instead, only a few specific studies are cited. Why are these ones chosen? We have no idea. To this extent I am not convinced that the references used here are the most appropriate.”

I have reviewed the existing references and incorporated additional sources. However, the study does not claim to conduct a systematic literature review; rather, it adopts an interpretative approach to literature analysis.

19. “Instances of the latter are the claim that ‘The most well-known initiatives at the moment are ResearchEquals and Octopus’ for which no evidence is provided, the claim that ‘we believe that journal-independent peer review is a special case of Model 3’ for which no further argument is provided, and the claim that ‘the function of being the "supreme judge" in deciding what is "good" and "bad" science is taken on by peer review’ for which neither is provided.

Thank you for your feedback. I have implemented a more rigorous approach to argumentation in response.

20. “A particular example of this weakness, which is perhaps of marginal importance to the overall paper but of strong interest to this reviewer is the rather odd engagement with history within the paper. It is titled "Evolution of Peer Review" but is really focussed on the contemporary state-of-play. Section 2 starts with a short history of peer review in scientific publishing, but that seems intended only to establish what is described as the 'traditional' model of peer review. Given that that short history had just shown how peer review had been continually changing in character over centuries - and indeed Kochetkov goes on to describe further changes - it is a little difficult to work out what 'traditional' might mean here; what was 'traditional' in 2010 was not the same as what was 'traditional' in 1970. It is not clear how seriously this history is being taken. Kochetkov has earlier written that "as early as the beginning of the 21st century, it was argued that the system of peer review is 'broken'" but of course criticisms - including fundamental criticisms - of peer review are much older than this. Overall, this use of history seems designed to privilege the experience of a particular moment in time, that coincides with the start of the metascience reform movement.”

While the paper addresses some aspects of peer review history, it does not provide a comprehensive examination of this topic. A clarifying statement to this effect has been included in the methodology section.

“… this section incorporates elements of historical analysis, it does not fully qualify as such because primary sources were not directly utilized. Instead, it functions as an interpretative literature review, and one that is intentionally concise, as a comprehensive history of peer review falls outside the scope of this research”.

21. “Section 2 also demonstrates some of the second weakness described, a rather loose structure. Having moved from a discussion of the history of peer review to detail the first model, 'traditional' peer review, it then also goes on to describe the problems of this model. This part of the paper is one of the best - and best - evidenced. Given the importance of it to the main thrust of the discussion it should probably have been given more space as a Section all on its own.”

This section (now Section 4) has been extended, see also previous comment.

22. “Another example is Section 4 on Modular Publishing, in which Kochetkov notes "Strictly speaking, modular publishing is primarily an innovative approach for the publishing workflow in general rather than specifically for peer review." Kochetkov says "This is why we have placed this innovation in a separate category" but if it is not an innovation in peer review, the bigger question is 'Why was it included in this article at all?'.”

Modular publishing has been combined with registered reports into the deconstructed publication group of models, now Section 5.1.

23. “One example of the imprecisions of language is as follows. The author also shifts between the terms 'scientific communication' and 'science communication' but, at least in many contexts familiar to this reviewer, these are not the same things, the former denoting science-internal dissemination of results through publication (which the author considers), conferences and the like (which the author specifically excludes) while the latter denotes the science-external public dissemination of scientific findings to non-technical audiences, which is entirely out of scope for this article.”

Thank you for your remark. As a non- native speaker, I initially did not grasp the distinction between the terms. However, I believe the phrase ‘scholarly communication’ is the most universally applicable term. This adjustment has now been incorporated into the text.

24. “A final note is that Section 3, while an interesting discussion, seems largely derivative from a typology of Waltman, with the addition of a consideration of whether a reform is 'radical' or 'incremental', based on how 'disruptive' the reform is. Given that this is inherently a subjective decision, I wonder if it might not have been more informative to consider 'disruptiveness' on a scale and plot it accordingly. This would allow for some range to be imagined for each reform as well; surely reforms might be more or less disruptive depending on how they are implemented. Given that each reform is considered against each model, it is somewhat surprising that this is not presented in a tabular or graphical form.”

Ultimately, I excluded this metric due to its current reliance on purely subjective judgment. Measuring 'disruptiveness', e.g., through surveys or interviews remains a task for future research.

25. “Reconceptualize this as an opinion piece. Where systematic evidence can be drawn upon to make points, use that, but don't be afraid to just present a discussion from what is clearly a well-informed author.”

I cannot definitively classify this work as an opinion piece. In fact, this manuscript synthesizes elements of a literature review, research article, and opinion essay. My idea was to integrate the strengths of all three genres.

26. “Reconsider the focus on history and 'evolution' if the point is about the current state of play and evaluation of reforms (much as I would always want to see more studies on the history and evolution of peer review).”

I have revised the title to better reflect the study’s scope and explicitly emphasize its focus on contemporary developments in the field.

“Peer Review at the Crossroads”

27. “Consider ways in which the typology might be expanded, even if at subordinate level.”

I have updated the typology and introduced the third tier, where it is applicable (see Fig.2).

Reviewer 3

28. “In my view, the biggest issue with the current peer review system is the low quality of reviews, but the manuscript only mentions this fleetingly. The current system facilitates publication bias, confirmation bias, and is generally very inconsistent. I think this is partly due to reviewers’ lack of accountability in such a closed peer review system, but I would be curious to hear the author’s ideas about this, more elaborately than they provide them as part of issue 2.

I have elaborated on this issue in the footnote.

29. “I’m missing a section in the introduction on what the goals of peer review are or should be. You mention issues with peer review, and these are mostly fair, but their importance is only made salient if you link them to the goals of peer review. The author does mention some functions of peer review later in the paper, but I think it would be good to expand that discussion and move it to a place earlier in the manuscript.”

The functions of peer review are summarized in the first paragraph of Introduction.

30. “Table 1 is intuitive but some background on how the author arrived at these categorizations would be welcome. When is something incremental and when is something radical? Why are some innovations included but not others (e.g., collaborative peer review, see https://content.prereview.org/how-collaborative-peer-review-can-transform-scientific-research/)?”

Collaborative peer review, namely, Prereview was mentioned in the context of Model 3 (Publish-Review-Curate). However, I have extended this part of the paper.

31“‘Training of reviewers through seminars and online courses is part of the strategies of many publishers. At the same time, we have not been able to find statistical data or research to assess the effectiveness of such training.’ (p. 5)  There is some literature on this, although not recent. See work by Sara Schroter for example, Schroter et al., 2004; Schroter et al., 2008)”

Thank you very much, I have added these studies and a few more recent ones.

32. “‘It should be noted that most initiatives aimed at improving the quality of peer review simultaneously increase the costs.’ (p. 7) This claim needs some support. Please explicate why this typically is the case and how it should impact our evaluations of these initiatives.”

I have moved this part to the Discussion section.

33. “I would rephrase “Idea of the study” in Figure 2 since the other models start with a tangible output (the manuscript). This is the same for registered reports where they submit a tangible report including hypotheses, study design, and analysis plan. In the same vein, I think study design in the rest of the figure might also not be the best phrasing. Maybe the author could use the terminology used by COS (Stage 1 manuscript, and Stage 2 manuscript, see Details & Workflow tab of https://www.cos.io/initiatives/registered-reports). Relatedly, “Author submits the first version of the manuscript” in the first box after the ‘Manuscript (report)’ node maybe a confusing phrase because I think many researchers see the first version of the manuscript as the stage 1 report sent out for stage 1 review.”

Thank you very much. Stage 1 and Stage 2 manuscripts look like suitable labelling solution.

34. “One pathway that is not included in Figure 2 is that authors can decide to not conduct the study when improvements are required. Relatedly, in the publish-review-curate model, is revising the manuscripts based on the reviews not optional as well? Especially in the case of

3a, authors can hardly be forced to make changes even though the reviews are posted on the platform.”

All the four models imply a certain level of generalization; thus, I tried to avoid redundant details. However, I have added this choice to the PRC model (now, Model 4).

35. “I think the author should discuss the importance of ‘open identities’ more. This factor is now not explicitly included in any of the models, while it has been found to be one of the main characteristics of peer review systems (Ross-Hellauer, 2017).”

This part has been extended.

36. “More generally, I was wondering why the author chose these three models and not others. What were the inclusion criteria for inclusion in the manuscript? Some information on the underlying process would be welcome, especially when claims like ‘However, we believe that journal-independent peer review is a special case of Model 3 (‘Publish-Review-Curate’).’ are made without substantiation.”

The study included four generalized models of peer review that involved some level of abstraction.

37. “Maybe it helps to outline the goals of the paper a bit more clearly in the introduction. This helps the reader to know what to expect.”

The Introduction has been revised including the goal and objectives.

38. “The Modular Publishing section is not inherently related to peer review models, as you mention in the first sentence of that paragraph. As such, I think it would be best to omit this section entirely to maintain the flow of the paper. Alternatively, you could shortly discuss it in the discussion section but a separate paragraph seems too much from my point of view.”

Modular publishing has been combined with registered reports into the fragmented publishing group of models, now in Section 5.

39. “Labeling model 3 as post-publication review might be confusing to some readers. I believe many researchers see post-publication review as researchers making comments on preprints, or submitting commentaries to journals. Those activities are substantially different from the publish-review-curate model so I think it is important to distinguish between these types.”

The label was changed into Publish- Review-Curate model.

40. “I do not think the conclusions drawn below Table 3 logically follow from the earlier text. For example, why are “all functions of scientific communication implemented most quickly and transparently in Model 3”? It could be that the entire process takes longer in Model 3 (e.g. because reviewers need more time), so that Model 1 and Model 2 lead to outputs quicker. The same holds for the following claim: ‘The additional costs arising from the independent assessment of information based on open reviews are more than compensated by the emerging opportunities for scientific pluralism.’ What is the empirical evidence for this? While I personally do think that Model 3 improves on Model 1, emphatic statements like this require empirical evidence. Maybe the author could provide some suggestions on how we can attain this evidence. Model 2 does have some empirical evidence underpinning its validity (see Scheel, Schijen, Lakens, 2021; Soderberg et al., 2021; Sarafoglou et al. 2022) but more meta-research inquiries into the effectiveness and cost-benefits ratio of registered reports would still be welcome in general.”

The Discussion section has been substantially revised to address this point. While I acknowledge the current scarcity of empirical studies on innovative peer review models, I have incorporated a critical discussion of this methodological gap. I am grateful for the suggested literature on RRs, which I have now integrated into the relevant subsection.

41. “What is the underlaying source for the claim that openness requires three conditions?”

I have made effort to clarify within the text that this reflects my personal stance.

42. “‘If we do not change our approach, science will either stagnate or transition into other forms of communication.’ (p. 2) I don’t think this claim is supported sufficiently strongly. While I agree there are important problems in peer review, I think would need to be a more in-depth and evidence-based analysis before claims like this can be made.”

The sentence has been rephrased.

43. “On some occasions, the author uses ‘we’ while the study is single authored.”

This has been fixed.

44. “Figure 1: The top-left arrow from revision to (re-)submission is hidden”

I have updated Figure 1.

45. “‘The low level of peer review also contributes to the crisis of reproducibility in scientific research (Stoddart, 2016).’ (p. 4) I assume the author means the low quality of peer review.”

This has been fixed.

46. “‘Although this crisis is due to a multitude of factors, the peer review system bears a significant responsibility for it.’ (p. 4) This is also a big claim that is not substantiated”

I have paraphrased this sentence as “While multiple factors drive this crisis, deficiencies in the peer review process remain a significant contributor.” and added a footnote.

47. “‘Software for automatic evaluation of scientific papers based on artificial intelligence (AI) has emerged relatively recently” (p. 5) The author could add RegCheck (https://regcheck.app/) here, even though it is still in development. This tool is especially salient in light of the finding that preregistration-paper checks are rarely done as part of reviews (see Syed, 2023)”

Thank you very much, I have added this information.

48. “There is a typo in last box of Figure 1 (‘decicion’ instead of ‘decision’). I also found typos in the second box of Figure 2, where ‘screns’ should be ‘screens’, and the author decision box where ‘desicion’ should be ‘decision’”

This has been fixed.

49. “Maybe it would be good to mention results blinded review in the first paragraph of 3.2. This is a form of peer review where the study is already carried out but reviewers are blinded to the results. See work by Locascio (2017), Grand et al. (2018), and Woznyj et al. (2018).”

Thanks, I have added this (now section 5.2)

50. “Is ‘Not considered for peer review’ in figure 3b not the same as rejected? I feel that it is rejected in the sense that neither the manuscript not the reviews will be posted on the platform.”

Changed into “Rejected”

51. “‘In addition to the projects mentioned, there are other platforms, for example, PREreview12, which departs even more radically from the traditional review format due to the decentralized structure of work.’ (p. 11) For completeness, I think it would be helpful to add some more information here, for example why exactly decentralization is a radical departure from the traditional model.”

I have extended this passage.

52. “‘However, anonymity is very conditional - there are still many “keys” left in the manuscript, by which one can determine, if not the identity of the author, then his country, research group, or affiliated organization.’ (p.11) I would opt for the neutral ‘their’ here instead of ‘his’, especially given that this is a paragraph about equity and inclusion.”

This has been fixed.

53. “‘Thus, “closeness” is not a good way to address biases.’ (p. 11) This might be a straw man argument because I don’t believe researchers have argued that it is a good method to combat biases. If they did, it would be good to cite them here. Alternatively, the sentence could be

omitted entirely.

I have omitted the sentence.

54. “I would start the Modular Publishing section with the definition as that allows readers to interpret the other statements better.”

Modular publishing has been combined with registered reports into the deconstructed publication group of models, now in Section 5, general definition added.

55. “It would be helpful if the Models were labeled (instead of using Model 1, Model 2, and Model 3) so that readers don’t have to think back what each model involved.”

All the models represent a kind of generalization, which is why non-detailed labels are used. The text labels may vary depending on the context.

56. “Table 2: ‘Decision making’ for the editor’s role is quite broad, I recommend to specify and include what kind of decisions need to be made.”

Changed into “Making accept/reject decisions”

57. “Table 2: ‘Aim of review’ – I believe the aim of peer review differs also within these models (see the ‘schools of thought’ the author mentions earlier), so maybe a statement on what the review entails would be a better way to phrase this.”

Changed into “What does peer review entail?”

58. “Table 2: One could argue that the object of the review’ in Registered Reports is also the manuscript as a whole, just in different stages. As such, I would phrase this differently.

Current wording fits your remark: “Manuscript in terms of study design and execution”

Reviewer 4

59. “Page 3: It’s hard to get a feel for the timeline given the dates that are described. We have peer review becoming standard after WWII (after 1945), definitively established by the second half of the century, an example of obligatory peer review starting in 1976, and in crisis by the end of the 20th century. I would consider adding examples that better support this timeline – did it become more common in specific journals before 1976? Was the crisis by the end of the 20th century something that happened over time or something that was already intrinsic to the institution? It doesn’t seem like enough time to get established and then enter crisis, but more details/examples could help make the timeline clear. Consider discussing the benefits of the traditional model of peer review.”

This section has been extended.

60. “Table 1 – Most of these are self-explanatory to me as a reader, but not all. I don’t know what a registered report refers to, and it stands to reason that not all of these innovations are familiar to all readers. You do go through each of these sections, but that’s not clear when I initially look at the table. Consider having a more informative caption. Additionally, the left column is “Course of changes” here but “Directions” in text. I’d pick one and go with it for consistency.”

Table 1 has been replaced by Figure 2. I have also extended text descriptions, added definitions.

61. “With some of these methods, there’s the ability to also submit to a regular journal. Going to a regular journal presumably would instigate a whole new round of review, which may or may not contradict the previous round of post-publication review and would increase the length of time to publication by going through both types. If someone has a goal to publish in a journal, what benefit would they get by going through the post-publication review first, given this extra time?”

Some of these platforms, e.g., F1000, Lifecycle Journal, replace conventional journal publishing. Modular publishing allows for step-by-step feedback from peers. An important advantage of RRs over other peer review models lies in their capacity to enhance research efficiency. By conducting peer review at Stage 1, researchers gain the opportunity to refine their study design or data collection protocols before empirical work begins. Other models of review can offer critiques such as "the study should have been conducted differently" without actionable opportunity for improvement. The key motivation for having my paper reviewed in MetaROR is the quality of peer review – I have never received so many comments, frankly! Moreover, platforms such as MetaROR usually have partnering journals.

62. “There’s a section talking about institutional change (page 14). It mentions that openness requires three conditions – people taking responsibility for scientific communication, authors and reviewers, and infrastructure. I would consider adding some discussion of readers and evaluators. Readers have to be willing to accept these papers as reliable, trustworthy, and respectable to read and use the information in them. Evaluators such as tenure committees and potential employers would need to consider papers submitted through these approaches as evidence of scientific scholarship for the effort to be worthwhile for scientists.”

I have omitted these conditions and employed the Moore’s Technology Adoption Life Cycle. Thank you very much for your comment!

63. Based on this overview, which seems somewhat skewed towards the merits of these methods (conflict of interest, limited perspective on downsides to new methods/upsides to old methods), I am not quite ready to accept this effort as equivalent of a regular journal and pre-publication peer review process. I look forward to learning more about the approach and seeing this review method in action and as it develops.

The Discussion section has been substantially revised to address this point. While I acknowledge the current scarcity of empirical studies on innovative peer review models, I have incorporated a critical discussion of this methodological gap.

Author response:

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

Reviewer #1 (Public review): 

Zhu and colleagues used high-density Neuropixel probes to perform laminar recordings in V1 while presenting either small stimuli that stimulated the classical receptive field (CRF) or large stimuli whose border straddled the RF to provide nonclassical RF (nCRF) stimulation. Their main question was to understand the relative contribution of feedforward (FF), feedback (FB), and horizontal circuits to border ownership (Bown), which they addressed by measuring crosscorrelation across layers. They found differences in cross-correlation between feedback/horizontal (FH) and input layers during CRF and nCRF stimulation. 

Although the data looks high quality and analyses look mostly fine, I had a lot of difficulty understanding the logic in many places. Examples of my concerns are written below. 

(1) What is the main question? The authors refer to nCRF stimulation emerging from either feedback from higher areas or horizontal connections from within the same area (e.g. lines 136 to 138 and again lines 223-232). I initially thought that the study would aim to distinguish between the two. However, the way the authors have clubbed the layers in 3D, the main question seems to be whether Bown is FF or FH (i.e., feedback and horizontal are clubbed). Is this correct? If so, I don't see the logic, since I can't imagine Bown to be purely FF. Thus, just showing differences between CRF stimulation (which is mainly expected to be FF) and nCRF stimulation is not surprising to me. 

We thank the reviewer for their thoughtful comments. As explained in the discussion, we grouped cortical layers to reduce uncertainty in precisely assigning laminar boundaries and to increase statistical power. Consequently, this limits our ability to distinguish the relative contributions of feedback inputs, primarily targeting layers 1 and 6, and horizontal connections, mainly within layers 2/3 and 5. Nevertheless, previous findings, especially regarding the rapid emergence of B_own signals, suggest that feedback is more biologically plausible than horizontal-based mechanisms.

Importantly, the emergence of B_own signals in the primate brain should not be taken for granted. Direct physiological evidence that distinguishes feedforward from feedback/horizontal mechanisms has been lacking. While we agree it is unlikely that B_own is mediated solely by feedforward processing, we felt it was necessary to test this empirically, particularly using highresolution laminar recordings.

As discussed, feedforward models of B_own have been proposed (e.g., Super, Romeo, and Keil, 2010; Saki and Nishimura, 2006). These could, in theory, be supported by more general nCRF modulations arising through early feedforward inhibitions, such as those observed in the retinogeniculate pathway (e.g., Webb, Tinsley, Vincent and Derrington, 2005; Blitz and Regehr, 2005; Alitto and Usrey, 2008). However, most B_own models rely heavily on response latency, yet very few studies have recorded across layers or areas simultaneously to address this directly. Notably, recent findings in area V4 show that B_own signals emerge earlier in deep layers than in granular (input) layers, suggesting a non-feedforward origin (Franken and Reynolds, 2021).

Furthermore, although previous studies have shown that the nCRF can modulate firing rates and the timing of neuronal firing across layers, our findings go beyond these effects. We provide clear evidence that nCRF modulation also alters precise spike timing relationships and interlaminar coordination, and that the magnitude of nCRF modulation depends on these interlaminar interactions. This supports the idea that B_own , or more general nCRF modulation, involves more than local rate changes, reflecting layer-specific network dynamics consistent with feedback or lateral integration.

(2) Choice of layers for cross-correlation analysis: In the Introduction, and also in Figure 3C, it is mentioned that FF inputs arrive in 4C and 6, while FB/Horizontal inputs arrive at "superficial" and "deep", which I take as layer 2/3 and 5. So it is not clear to me why (i) layer 4A/B is chosen for analysis for Figure 3D (I would have thought layer 6 should have been chosen instead) and (ii) why Layers 5 and 6 are clubbed. 

We thank the reviewer for raising this important point. The confusion likely stems from our use of the terms “superficial” and “deep” layers when describing the targets of feedback/horizontal inputs. To clarify, by “superficial” and “deep,” we specifically refer to layers 1–3 and layers 5–6, respectively, as illustrated in Figure 3C. Feedback and horizontal inputs relatively avoid entire layer 4, including both 4C and 4A/B.

We also emphasize that the classification of layers as feedforward or feedback/horizontal recipients is relative rather than absolute. For example, although layer 6 receives both feedforward and feedback/horizontal inputs, it contains a higher proportion of feedback/horizontal inputs compared to layers 4C and 4A/B. 

We had addressed this rationale in the Discussion, but recognize it may not have been sufficiently emphasized. We have revised the main text accordingly to clarify this point for readers in the final manuscript version.

(3) Addressing the main question using cross-correlation analysis: I think the nice peaks observed in Figure 3B for some pairs show how spiking in one neuron affects the spiking in another one, with the delay in cross-correlation function arising from the conduction delay. This is shown nicely during CRF stimulation in Figure 3D between 4C -> 2/3, for example. However, the delay (positive or negative) is constrained by anatomical connectivity. For example, unless there are projections from 2/3 back to 4C which causes firing in a 2/3 layer neuron to cause a spike in a layer 4 neuron, we cannot expect to get a negative delay no matter what kind of stimulation (CRF versus nCRF) is used. 

We thank the reviewer for the insightful comment. The observation that neurons within FH_i laminar compartments (layers 2/3, 5/6) can lead those in layer 4 (4C, 4A/B) during nCRF stimulation may indeed seem unexpected. However, several anatomical pathways could mediate the propagation of B_own signals from FH_i compartments to layer 4. We have revised the Discussion section in the final version of the manuscript to address this point explicitly.

In Macaque V1, projections from layers 2/3 to 4A/B have been documented (Blasdel et al., 1985; Callaway and Wiser, 1996), and neurons in 4A/B often extend apical dendrites into layers 2/3 (Lund, 1988; Yoshioka et al., 1994). Although direct projections from layers 2/3 to 4C are generally sparse (Callaway, 1998), a subset of neurons in the lower part of layer 3 can give off collateral axons to 4C (Lund and Yoshioka, 1991). Additionally, some 4C neurons extend dendrites into 4B, enabling potential dendritic integration of inputs from more superficial layers (Somogyi and Cowey, 1981; Mates and Lund, 1983; Yabuta and Callaway, 1998). Sparse connections from 2/3 to layer 4 have also been reported in cat V1 (Binzegger, Douglas and Martin, 2004). Moreover, layers 2/3 may influence 4C neurons disynaptically, without requiring dense monosynaptic connections. 

Importantly, while CCGs can suggest possible circuit arrangements, functional connectivity may arise through mechanisms not fully captured by traditional anatomical tracing. Indeed, the apparent discrepancy between anatomical and functional data is not uncommon. For example, although 4B is known to receive anatomical input primarily from 4Cα, but not 4Cβ, photostimulation experiments have shown that 4B neurons can also be functionally driven by 4Cβ (Sawatari and Callaway, 1996). Our observation of functional inputs from layers 2/3 to layer 4 is also consistent with prior findings in rodent V1, where CCG analysis (e.g., Figure 7 in Senzai, Fernandez-Ruiz and Buzsaki, 2019) or photostimulation (Xu et al., 2016) revealed similar pathways. 

Layers 5/6 provide dense projections to layers 4A/B (Lund, 1988; Callaway, 1998). In particular, layer 6 pyramidal neurons, especially the subset classified as Type 1 cells, project substantially to layer 4C (Wiser and Callaway, 1996; Fitzpatrick et al., 1985). 

Reviewer #2 (Public review): 

Summary: 

The authors present a study of how modulatory activity from outside the classical receptive field (cRF) differs from cRF stimulation. They study neural activity across the different layers of V1 in two anesthetized monkeys using Neuropixels probes. The monkeys are presented with drifting gratings and border-ownership tuning stimuli. They find that border-ownership tuning is organized into columns within V1, which is unexpected and exciting, and that the flow of activity from cellto-cell (as judged by cross-correlograms between single units) is influenced by the type of visual stimulus: border-ownership tuning stimuli vs. drifting-grating stimuli. 

Strengths: 

The questions addressed by the study are of high interest, and the use of Neuropixels probes yields extremely high numbers of single-units and cross-correlation histograms (CCHs) which makes the results robust. The study is well-described. 

Weaknesses: 

The weaknesses of the study are (a) the use of anesthetized animals, which raises questions about the nature of the modulatory signal being measured and the underlying logic of why a change in visual stimulus would produce a reversal in information flow through the cortical microcircuit and (b) the choice of visual stimuli, which do not uniquely isolate feedforward from feedback influences. 

(1) The modulation latency seems quite short in Figure 2C. Have the authors measured the latency of the effect in the manuscript and how it compares to the onset of the visually driven response? It would be surprising if the latency was much shorter than 70ms given previous measurements of BO and figure-ground modulation latency in V2 and V1. On the same note, it might be revealing to make laminar profiles of the modulation (i.e. preferred - non-preferred border orientation) as it develops over time. Does the modulation start in feedback recipient layers? 

(2) Can the authors show the average time course of the response elicited by preferred and nonpreferred border ownership stimuli across all significant neurons? 

We thank the reviewer for the insightful comment—this is indeed an important and often overlooked point. As noted in the Discussion, B_own modulation differs from other forms of figure-ground modulation (e.g., Lamme et al., 1998) in that it can emerge very rapidly in early visual cortex—within ~10–35 ms after response onset (Zhou et al., 2000; Sugihara et al., 2011). This rapid emergence has been interpreted as evidence for the involvement of fast feedback inputs, which can propagate up to ten times faster than horizontal connections (Girard et al., 2001). Moreover, interlaminar interactions via monosynaptic or disynaptic connections can occur on very short timescales (a few milliseconds), further complicating efforts to disentangle feedback influences based solely on latency.

Thus, while the early onset of modulation in our data may appear surprising, it is consistent with prior B_own findings, and likely reflects a combination of fast feedback and rapid interlaminar processing. This makes it challenging to use conventional latency measurements to resolve laminar differences in B_own modulation. Latency comparisons are well known to be susceptible to confounds such as variability in response onset, luminance, contrast, stimulus size, and other sensory parameters. 

Although we did not explicitly quantify the latency of B_own modulation in this manuscript, our cross-correlation analysis provides a more sensitive and temporally resolved measure of interlaminar information flow. We therefore focused on this approach rather than laminar modulation profiles, as it more directly addresses our primary research question.

(3) The logic of assuming that cRF stimulation should produce the opposite signal flow to borderownership tuning stimuli is worth discussing. I suspect the key difference between stimuli is that they used drifting gratings as the cRF stimulus, the movement of the stimulus continually refreshes the retinal image, leading to continuous feedforward dominance of the signals in V1. Had they used a static grating, the spiking during the sustained portion of the response might also show more influence of feedback/horizontal connections. Do the initial spikes fired in response to the borderownership tuning stimuli show the feedforward pattern of responses? The authors state that they did not look at cross-correlations during the initial response, but if they do, do they see the feedforward-dominated pattern? The jitter CCH analysis might suffice in correcting for the response transient. 

We thank the reviewer for the insightful comment. As noted in the final Results section, our CRF and nCRF stimulation paradigms differ in respects beyond the presence or absence of nonclassical modulation, including stimulus properties within the CRF.

We agree with the reviewer’s speculation that drifting gratings may continually refresh the retinal image, promoting sustained feedforward dominance in V1, whereas static gratings might allow greater influence from feedback/horizontal inputs during the sustained response. Likewise, the initial response to the B_own stimulus could be dominated by feedforward activity before feedback/horizontal influences arrive. 

This contrast was a central motivation for our experimental design: we deliberately used two stimulus conditions — drifting gratings to emphasize feedforward processing, and B_own stimuli, which are known to engage feedback modulation — to test whether these two conditions yield different patterns of interlaminar information flow. Our results confirm that they do. While we did not separately analyze the very initial spike period, our focus is on interlaminar information flow during the sustained response, which serves as the primary measure of feedback/horizontal engagement in this study.

Finally, beyond this direct comparison, we show in Figure 5 that under nCRF stimulation alone, the direction and strength of interlaminar information flow correlate with the magnitude of B_own modulation, further supporting the idea that our cross-correlation approach reveals functionally meaningful differences in cortical processing.

(4) The term "nCRF stimulation" is not appropriate because the CRF is stimulated by the light/dark edge. 

We thank the reviewer for the comment. As noted in the Introduction, nCRF effects described in the literature invariably involve stimulation both inside and outside the CRF. Our use of the term “nCRF stimulation” refers to this experimental paradigm, rather than suggesting that the CRF itself is unstimulated. We hope this clarifies our use of the term.

Reviewer #3 (Public review): 

Summary: 

The paper by Zhu et al is on an important topic in visual neuroscience, the emergence in the visual cortex of signals about figures and ground. This topic also goes by the name border ownership. The paper utilizes modern recording techniques very skillfully to extend what is known about border ownership. It offers new evidence about the prevalence of border ownership signals across different cortical layers in V1 cortex. Also, it uses pairwise cross-correlation to study signal flow under different conditions of visual stimulation that include the border ownership paradigm. 

Strengths: 

The paper's strengths are its use of multi-electrode probes to study border ownership in many neurons simultaneously across the cortical layers in V1, and its innovation of using crosscorrelation between cortical neurons -- when they are viewing border-ownership patterns or instead are viewing grating patterns restricted to the classical receptive field (CRF). 

Weaknesses: 

The paper's weaknesses are its largely incremental approach to the study of border ownership and the lack of a critical analysis of the cross-correlation data. The paper as it is now does not advance our understanding of border ownership; it mainly confirms prior work, and it does not challenge or revise consensus beliefs about mechanisms. However, it is possible that, in the rich dataset the authors have obtained, they do possess data that could be added to the paper to make it much stronger. 

Critique: 

The border ownership data on V1 offered in the paper replicates experimental results obtained by Zhou and von der Heydt (2000) and confirms the earlier results using the same analysis methods as Zhou. The incremental addition is that the authors found border ownership in all cortical layers extending Zhou's results that were only about layer 2/3. 

The cross-correlation results show that the pattern of the cross-correlogram (CCG) is influenced by the visual pattern being presented. However, the results are not analyzed mechanistically, and the interpretation is unclear. For instance, the authors show in Figure 3 (and in Figure S2) that the peak of the CCG can indicate layer 2/3 excites layer 4C when the visual stimulus is the border ownership test pattern, a large square 8 deg on a side. But how can layer 2/3 excite layer 4C? The authors do not raise or offer an answer to this question. Similar questions arise when considering the CCG of layer 4A/B with layer 2/3. What is the proposed pathway for layer 2/3 to excite 4A/B? Other similar questions arise for all the interlaminar CCG data that are presented. What known functional connections would account for the measured CCGs? 

We thank the reviewer for raising this important point. As noted in our response to a previous comment, several anatomical pathways could mediate apparent functional inputs from layers 2/3 to 4C and 4A/B. In macaque V1, projections from layers 2/3 to 4A/B have been documented (Blasdel et al., 1985; Callaway and Wiser, 1996), and neurons in 4A/B often extend apical dendrites into layers 2/3 (Lund, 1988; Yoshioka et al., 1994). Although direct projections from layers 2/3 to 4C are generally sparse (Callaway, 1998), a subset of lower layer 3 neurons can give off collateral axons to 4C (Lund and Yoshioka, 1991). Some 4C neurons also extend dendrites into 4B, potentially allowing dendritic integration of inputs from more superficial layers (Somogyi and Cowey, 1981; Mates and Lund, 1983; Yabuta and Callaway, 1998). Sparse connections from 2/3 to layer 4 have also been reported in cat V1 (Binzegger et al., 2004).

Moreover, layers 2/3 may influence 4C neurons disynaptically, without requiring dense monosynaptic connections. While CCGs suggest possible circuit arrangements, functional connectivity may arise through mechanisms not fully captured by anatomical tracing, and apparent discrepancies between anatomical and functional data are not uncommon. For example, although 4B is known to receive anatomical input primarily from 4Cα, 4B neurons can also be functionally driven by 4Cβ using photostimulation (Sawatari and Callaway, 1996). Our observation of functional inputs from layers 2/3 to layer 4 is also consistent with prior findings in rodent V1, where CCG analysis (e.g., Figure 7 in Senzai, Fernandez-Ruiz and Buzsaki, 2019) or photostimulation (Xu et al., 2016) revealed similar pathways. 

Layers 5/6 also provide dense projections to layers 4A/B (Lund, 1988; Callaway, 1998). In particular, layer 6 pyramidal neurons, especially the subset classified as Type 1 cells, project substantially to layer 4C (Wiser and Callaway, 1996; Fitzpatrick et al., 1985). 

We have revised the Discussion section to explicitly address these points and clarify the potential anatomical and functional pathways underlying the measured interlaminar CCGs, highlighting how inputs from layers 2/3 and 5/6 to layer 4 can be mediated via both direct and indirect connections.

The problems in understanding the CCG data are indirectly caused by the lack of a critical analysis of what is happening in the responses that reveal the border ownership signals, as in Figure 2. Let's put it bluntly - are border ownership signals excitatory or inhibitory? The reason I raise this question is that the present authors insightfully place border ownership as examples of the action of the non-classical receptive field (nCRF) of cortical cells. Most previous work on the nCRF (many papers cited by the authors) reveal the nCRF to be inhibitory or suppressive. In order to know whether nCRF signals are excitatory or inhibitory, one needs a baseline response from the CRF, so that when you introduce nCRF signals you can tell whether the change with respect to the CRF is up or down. As far as I know, prior work on border ownership has not addressed this question, and the present paper doesn't either. This is where the rich dataset that the present authors possess might be used to establish a fundamental property of border ownership. 

Then we must go back to consider what the consequences of knowing the sign of the border ownership signal would mean for interpreting the CCG data. If the border ownership signals from extrastriate feedback or, alternatively, from horizontal intrinsic connections, are excitatory, they might provide a shared excitatory input to pairs of cells that would show up in the CCG as a peak at 0 delay. However, if the border ownership manuscript signals are inhibitory, they might work by exciting only inhibitory neurons in V1. This could have complicated consequences for the CCG.The interpretation of the CCG data in the present version of the m is unclear (see above). Perhaps a clearer interpretation could be developed once the authors know better what the border ownership signals are. 

We thank the reviewer for raising this fundamental and thought-provoking question. As noted, B_own signals arise from nCRF, which has often been associated with suppressive effects. However, Zhang and von der Heydt (2010) provided important insight into this issue by systematically varying the placement of figure fragments outside the CRF while keeping an edge centered within the CRF. They found that contextual fragments on the preferred side of B_own produce facilitation, while those on the non-preferred side produce suppression. Thus, the nCRF contribution to B_own reflects both excitatory and inhibitory modulation, depending on the spatial configuration of the figure.

These effects were well explained by their model in which feedback from grouping cells in higher areas selectively enhances or suppresses V1/V2 neuron responses, depending on their B_own preference. In this framework, the B_own signal itself is not inherently excitatory or inhibitory; rather, it results from the net effect of feedback, which can be either facilitative or suppressive. Importantly, it is the input that is modulated — not that the receiving neurons are necessarily inhibitory themselves.

In the current study, our analysis focused on CCGs showing excessive coincident spiking, i.e., positive peaks, which are typically interpreted as evidence for shared excitatory input or excitatory connections. Due to the limited number of connections, we did not analyze inhibitory interactions, such as anti-correlations or delayed suppression in the CCGs, which would be expected if the reference neuron were inhibitory. Therefore, the CCGs we report here likely reflect the excitatory component of the B_own signal, and possibly its upstream drive via feedback. While a full separation of excitatory and inhibitory components remains an important goal for future work, our data suggest that B_own modulation is at least partially mediated through excitatory feedback input.

My critique of the CCG analysis applies to Figure 5 also. I cannot comprehend the point of showing a very weak correlation of CCG asymmetry with Border Ownership Index, especially when what CCG asymmetry means is unclear mechanistically. Figure 5 does not make the paper stronger in my opinion. 

We thank the reviewer for this comment. As described in the Results section for Figure 5, the observation that interlaminar information flow correlates with B_own modulation is important because it demonstrates that these flow patterns are specifically related to the magnitude of B_own signals, independent of the comparisons between CRF and nCRF stimulation. 

In Figure 3, the authors show two CCGs that involve 4C--4C pairs. It would be nice to know more about such pairs. If there are any 6--6 pairs, what they look like also would be interesting. The authors also in Figure 3 show CCG's of two 4C--4A/B pairs and it would be quite interesting to know how such CCGs behave when CRF and nCRF stimuli are compared. In other words, the authors have shown us they have many data but have chosen not to analyze them further or to explain why they chose not to analyze them. It might help the paper if the authors would present all the CCG types they have. This suggestion would be helpful when the authors know more about the sign of border ownership signals, as discussed at length above. 

We thank the reviewer for the insightful comment. The rationale for selecting specific laminar pairs is described in the Results section after Figure 3C and further discussed in the Discussion. In brief, we focused on CCGs computed from pairs in which one neuron resided in laminar compartments receiving feedback/horizontal inputs (layers 2/3 and 5/6) and the other within compartments relatively devoid of these inputs (layers 4C and 4A/B).

To mitigate uncertainty in defining exact laminar boundaries and to maximize statistical power, we combined some anatomical layers into distinct laminar compartments. This approach allowed us to compare the relative spike timing between neuronal pairs during CRF and nCRF stimulation. If feedback/horizontal inputs contribute more during nCRF than CRF stimulation, we expect this to be reflected in the lead-lag relationships of the CCGs. While other pairs (e.g., 5/6–5/6 or 4C– 4A/B) could in principle be analyzed, the hypothesized patterns for these pairs are less clear, and thus they were not the focus of our study. Nonetheless, these additional pairs represent interesting directions for future work.

Author response:

The following is the authors’ response to the original reviews

We thank all the reviewers for their constructive comments. We have carefully considered your feedback and revised the manuscript accordingly. The major concern raised was the applicability of SegPore to the RNA004 dataset. To address this, we compared SegPore with f5c and Uncalled4 on RNA004, and found that SegPore demonstrated improved performance, as shown in Table 2 of the revised manuscript.

Following the reviewers’ recommendations, we updated Figures 3 and 4. Additionally, we added one table and three supplementary figures to the revised manuscript:

· Table 2: Segmentation benchmark on RNA004 data

· Supplementary Figure S4: RNA translocation hypothesis illustrated on RNA004 data

· Supplementary Figure S5: Illustration of Nanopolish raw signal segmentation with eventalign results

· Supplementary Figure S6: Running time of SegPore on datasets of varying sizes

Below, we provide a point-by-point response to your comments.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors describe a new computational method (SegPore), which segments the raw signal from nanopore-direct RNA-Seq data to improve the identification of RNA modifications. In addition to signal segmentation, SegPore includes a Gaussian Mixture Model approach to differentiate modified and unmodified bases. SegPore uses Nanopolish to define a first segmentation, which is then refined into base and transition blocks. SegPore also includes a modification prediction model that is included in the output. The authors evaluate the segmentation in comparison to Nanopolish and Tombo, and they evaluate the impact on m6A RNA modification detection using data with known m6A sites. In comparison to existing methods, SegPore appears to improve the ability to detect m6A, suggesting that this approach could be used to improve the analysis of direct RNA-Seq data.

Strengths:

SegPore addresses an important problem (signal data segmentation). By refining the signal into transition and base blocks, noise appears to be reduced, leading to improved m6A identification at the site level as well as for single-read predictions. The authors provide a fully documented implementation, including a GPU version that reduces run time. The authors provide a detailed methods description, and the approach to refine segments appears to be new.

Weaknesses:

In addition to Nanopolish and Tombo, f5c and Uncalled4 can also be used for segmentation, however, the comparison to these methods is not shown.

The method was only applied to data from the RNA002 direct RNA-Sequencing version, which is not available anymore, currently, it remains unclear if the methods still work on RNA004.

Thank you for your comments.

To clarify the background, there are two kits for Nanopore direct RNA sequencing: RNA002 (the older version) and RNA004 (the newer version). Oxford Nanopore Technologies (ONT) introduced the RNA004 kit in early 2024 and has since discontinued RNA002. Consequently, most public datasets are based on RNA002, with relatively few available for RNA004 (as of 30 June 2025).

Nanopolish and Tombo were developed for raw signal segmentation and alignment using RNA002 data, whereas f5c and Uncalled4are the only two software supporting RNA004 data.  Since the development of SegPore began in January 2022, we initially focused on RNA002 due to its data availability. Accordingly, our original comparisons were made against Nanopolish and Tombo using RNA002 data.

We have now updated SegPore to support RNA004 and compared its performance against f5c and Uncalled4 on three public RNA004 datasets.

As shown in Table 2 of the revised manuscript, SegPore outperforms both f5c and Uncalled4 in raw signal segmentation. Moreover, the jiggling translocation hypothesis underlying SegPore is further supported, as shown in Supplementary Figure S4.

The overall improvement in accuracy appears to be relatively small.

Thank you for the comment.

We understand that the improvements shown in Tables 1 and 2 may appear modest at first glance due to the small differences in the reported standard deviation (std) values. However, even small absolute changes in std can correspond to substantial relative reductions in noise, especially when the total variance is low.

To better quantify the improvement, we assume that approximately 20% of the std for Nanopolish, Tombo, f5c, and Uncalled4 arises from noise. Using this assumption, we calculate the relative noise reduction rate of SegPore as follows:

Noise reduction rate = (baseline std − SegPore std) / (0.2 × baseline std) ​​

Based on this formula, the average noise reduction rates across all datasets are:

- SegPore vs Nanopolish: 49.52%

- SegPore vs Tombo: 167.80%

- SegPore vs f5c: 9.44%

- SegPore vs Uncalled4: 136.70%

These results demonstrate that SegPore can reduce the noise level by at least 9% given a noise level of 20%, which we consider a meaningful improvement for downstream tasks, such as base modification detection and signal interpretation. The high noise reduction rates observed in Tombo and Uncalled4 (over 100%) suggest that their actual noise proportion may be higher than our 20% assumption.

We acknowledge that this 20% noise level assumption is an approximation. Our intention is to illustrate that SegPore provides measurable improvements in relative terms, even when absolute differences appear small.

The run time and resources that are required to run SegPore are not shown, however, it appears that the GPU version is essential, which could limit the application of this method in practice.

Thank you for your comment.

Detailed instructions for running SegPore are provided in github (https://github.com/guangzhaocs/SegPore). Regarding computational resources, SegPore currently requires one CPU core and one Nvidia GPU to perform the segmentation task efficiently.

We present SegPore’s runtime for typical datasets in Supplementary Figure S6 in the revised manuscript.  For a typical 1 GB fast5 file, the segmentation takes approximately 9.4 hours using a single NVIDIA DGX‑1 V100 GPU and one CPU core.

Currently, GPU acceleration is essential to achieve practical runtimes with SegPore. We acknowledge that this requirement may limit accessibility in some environments. To address this, we are actively working on a full C++ implementation of SegPore that will support CPU-only execution. While development is ongoing, we aim to release this version in a future update.

Reviewer #2 (Public review):

Summary:

The work seeks to improve the detection of RNA m6A modifications using Nanopore sequencing through improvements in raw data analysis. These improvements are said to be in the segmentation of the raw data, although the work appears to position the alignment of raw data to the reference sequence and some further processing as part of the segmentation, and result statistics are mostly shown on the 'data-assigned-to-kmer' level.

As such, the title, abstract, and introduction stating the improvement of just the 'segmentation' does not seem to match the work the manuscript actually presents, as the wording seems a bit too limited for the work involved.

The work itself shows minor improvements in m6Anet when replacing Nanopolish eventalign with this new approach, but clear improvements in the distributions of data assigned per kmer. However, these assignments were improved well enough to enable m6A calling from them directly, both at site-level and at read-level.

Strengths:

A large part of the improvements shown appear to stem from the addition of extra, non-base/kmer specific, states in the segmentation/assignment of the raw data, removing a significant portion of what can be considered technical noise for further analysis. Previous methods enforced the assignment of all raw data, forcing a technically optimal alignment that may lead to suboptimal results in downstream processing as data points could be assigned to neighbouring kmers instead, while random noise that is assigned to the correct kmer may also lead to errors in modification detection.

For an optimal alignment between the raw signal and the reference sequence, this approach may yield improvements for downstream processing using other tools.<br /> Additionally, the GMM used for calling the m6A modifications provides a useful, simple, and understandable logic to explain the reason a modification was called, as opposed to the black models that are nowadays often employed for these types of tasks.

Weaknesses:

The work seems limited in applicability largely due to the focus on the R9's 5mer models. The R9 flow cells are phased out and not available to buy anymore. Instead, the R10 flow cells with larger kmer models are the new standard, and the applicability of this tool on such data is not shown. We may expect similar behaviour from the raw sequencing data where the noise and transition states are still helpful, but the increased kmer size introduces a large amount of extra computing required to process data and without knowledge of how SegPore scales, it is difficult to tell how useful it will really be. The discussion suggests possible accuracy improvements moving to 7mers or 9mers, but no reason why this was not attempted.

Thank you for pointing out this important limitation. Please refer to our response to Point 1 of Reviewer 1 for SegPore’s performance on RNA004 data. Notably, the jiggling behavior is also observed in RNA004 data, and SegPore achieves better performance than both f5c and Uncalled4.

The increased k-mer size in RNA004 affects only the training phase of SegPore (refer to Supplementary Note 1, Figure 5 for details on the training and testing phases). Once the baseline means and standard deviations for each k-mer are established, applying SegPore to RNA004 data proceeds similarly to RNA002. This is because each k-mer in the reference sequence has, at most, two states (modified and unmodified). While the larger k-mer size increases the size of the parameter table, it does not increase the computational complexity during segmentation. Although estimating the initial k-mer parameter table requires significant time and effort on our part, it does not affect the runtime for end users applying SegPore to RNA004 data.

Extending SegPore from 5-mers to 7-mers or 9-mers for RNA002 data would require substantial effort to retrain the model and generate sufficient training data. Additionally, such an extension would make SegPore’s output incompatible with widely used upstream and downstream tools such as Nanopolish and m6Anet, complicating integration and comparison. For these reasons, we leave this extension for future work.

The manuscript suggests the eventalign results are improved compared to Nanopolish. While this is believably shown to be true (Table 1), the effect on the use case presented, downstream differentiation between modified and unmodified status on a base/kmer, is likely limited as during actual modification calling the noisy distributions are usually 'good enough', and not skewed significantly in one direction to really affect the results too terribly.

Thank you for your comment. While current state-of-the-art (SOTA) methods perform well on benchmark datasets, there remains significant room for improvement. Most SOTA evaluations are based on limited datasets, primarily covering DRACH motifs in human and mouse transcriptomes. However, m6A modifications can also occur in non-DRACH motifs, where current models may underperform. Additionally, other RNA modifications—such as pseudouridine, inosine, and m5C—are less studied, and their detection may benefit from improved signal modeling.

We would also like to emphasize that raw signal segmentation and RNA modification detection are distinct tasks. SegPore focuses on the former, providing a cleaner, more interpretable signal that can serve as a foundation for downstream tasks. Improved segmentation may facilitate the development of more accurate RNA modification detection algorithms by the community.

Scientific progress often builds incrementally through targeted improvements to foundational components. We believe that enhancing signal segmentation, as SegPore does, contributes meaningfully to the broader field—the full impact will become clearer as the tool is adopted into more complex workflows.

Furthermore, looking at alternative approaches where this kind of segmentation could be applied, Nanopolish uses the main segmentation+alignment for a first alignment and follows up with a form of targeted local realignment/HMM test for modification calling (and for training too), decreasing the need for the near-perfect segmentation+alignment this work attempts to provide. Any tool applying a similar strategy probably largely negates the problems this manuscript aims to improve upon.

We thank the reviewer for this insightful comment.

To clarify, Nanopolish provides three independent commands: polya, eventalign, and call-methylation.

- The polya command identifies the adapter, poly(A) tail, and transcript region in the raw signal.

- The eventalign command aligns the raw signal to a reference sequence, assigning a signal segment to individual k-mers in the reference.

- The call-methylation command detects methylated bases from DNA sequencing data.

The eventalign command corresponds to “the main segmentation+alignment for a first alignment,” while call-methylation corresponds to “a form of targeted local realignment/HMM test for modification calling,” as mentioned in the reviewer’s comment. SegPore’s segmentation is similar in purpose to Nanopolish’s eventalign, while its RNA modification estimation component is similar in concept to Nanopolish’s call-methylation.

We agree the general idea may appear similar, but the implementations are entirely different. Importantly, Nanopolish’s call-methylation is designed for DNA sequencing data, and its models are not trained to recognize RNA modifications. This means they address distinct research questions and cannot be directly compared on the same RNA modification estimation task. However, it is valid to compare them on the segmentation task, where SegPore exhibits better performance (Table 1).

We infer the reviewer may suggest that because m6Anet is a deep neural network capable of learning from noisy input, the benefit of more accurate segmentation (such as that provided by SegPore) might be limited. This concern may arise from the limited improvement of SegPore+m6Anet over Nanopolish+m6Anet in bulk analysis (Figure 3). Several factors may contribute to this observation:

(i) For reads aligned to the same gene in the in vivo data, alignment may be inaccurate due to pseudogenes or transcript isoforms.

(ii) The in vivo benchmark data are inherently more complex than in vitro datasets and may contain additional modifications (e.g., m5C, m7G), which can confound m6A calling by altering the signal baselines of k-mers.

(iii) m6Anet is trained on events produced by Nanopolish and may not be optimal for SegPore-derived events.

(iv) The benchmark dataset lacks a modification-free (IVT) control sample, making it difficult to establish a true baseline for each k-mer.

In the IVT data (Figure 4), SegPore shows a clear improvement in single-molecule m6A identification, with a 3~4% gain in both ROC-AUC and PR-AUC. This demonstrates SegPore’s practical benefit for applications requiring higher sensitivity at the molecule level.

As noted earlier, SegPore’s contribution lies in denoising and improving the accuracy of raw signal segmentation, which is a foundational step in many downstream analyses. While it may not yet lead to a dramatic improvement in all applications, it already provides valuable insights into the sequencing process (e.g., cleaner signal profiles in Figure 4) and enables measurable gains in modification detection at the single-read level. We believe SegPore lays the groundwork for developing more accurate and generalizable RNA modification detection tools beyond m6A.

We have also added the following sentence in the discussion to highlight SegPore’s limited performance in bulk analysis:

“The limited improvement of SegPore combined with m6Anet over Nanopolish+m6Anet in bulk in vivo analysis (Figure 3) may be explained by several factors: potential alignment inaccuracies due to pseudogenes or transcript isoforms, the complexity of in vivo datasets containing additional RNA modifications (e.g., m5C, m7G) affecting signal baselines, and the fact that m6Anet is specifically trained on events produced by Nanopolish rather than SegPore. Additionally, the lack of a modification-free control (in vitro transcribed) sample in the benchmark dataset makes it difficult to establish true baselines for each k-mer. Despite these limitations, SegPore demonstrates clear improvement in single-molecule m6A identification in IVT data (Figure 4), suggesting it is particularly well suited for in vitro transcription data analysis.”

Finally, in the segmentation/alignment comparison to Nanopolish, the latter was not fitted(/trained) on the same data but appears to use the pre-trained model it comes with. For the sake of comparing segmentation/alignment quality directly, fitting Nanopolish on the same data used for SegPore could remove the influences of using different training datasets and focus on differences stemming from the algorithm itself.

In the segmentation benchmark (Table 1), SegPore uses the fixed 5-mer parameter table provided by ONT. The hyperparameters of the HHMM are also fixed and not estimated from the raw signal data being segmented. Only in the m6A modification task,  SegPore does perform re-estimation of the baselines for the modified and unmodified states of k-mers. Therefore, the comparison with Nanopolish is fair, as both tools rely on pre-defined models during segmentation.

Appraisal:

The authors have shown their method's ability to identify noise in the raw signal and remove their values from the segmentation and alignment, reducing its influences for further analyses. Figures directly comparing the values per kmer do show a visibly improved assignment of raw data per kmer. As a replacement for Nanopolish eventalign it seems to have a rather limited, but improved effect, on m6Anet results. At the single read level modification modification calling this work does appear to improve upon CHEUI.

Impact:

With the current developments for Nanopore-based modification largely focusing on Artificial Intelligence, Neural Networks, and the like, improvements made in interpretable approaches provide an important alternative that enables a deeper understanding of the data rather than providing a tool that plainly answers the question of whether a base is modified or not, without further explanation. The work presented is best viewed in the context of a workflow where one aims to get an optimal alignment between raw signal data and the reference base sequence for further processing. For example, as presented, as a possible replacement for Nanopolish eventalign. Here it might enable data exploration and downstream modification calling without the need for local realignments or other approaches that re-consider the distribution of raw data around the target motif, such as a 'local' Hidden Markov Model or Neural Networks. These possibilities are useful for a deeper understanding of the data and further tool development for modification detection works beyond m6A calling.

Reviewer #3 (Public review):

Summary:

Nucleotide modifications are important regulators of biological function, however, until recently, their study has been limited by the availability of appropriate analytical methods. Oxford Nanopore direct RNA sequencing preserves nucleotide modifications, permitting their study, however, many different nucleotide modifications lack an available base-caller to accurately identify them. Furthermore, existing tools are computationally intensive, and their results can be difficult to interpret.

Cheng et al. present SegPore, a method designed to improve the segmentation of direct RNA sequencing data and boost the accuracy of modified base detection.

Strengths:

This method is well-described and has been benchmarked against a range of publicly available base callers that have been designed to detect modified nucleotides.

Weaknesses:

However, the manuscript has a significant drawback in its current version. The most recent nanopore RNA base callers can distinguish between different ribonucleotide modifications, however, SegPore has not been benchmarked against these models.

I recommend that re-submission of the manuscript that includes benchmarking against the rna004_130bps_hac@v5.1.0 and rna004_130bps_sup@v5.1.0 dorado models, which are reported to detect m5C, m6A_DRACH, inosine_m6A and PseU.<br /> A clear demonstration that SegPore also outperforms the newer RNA base caller models will confirm the utility of this method.

Thank you for highlighting this important limitation. While Dorado, the new ONT basecaller, is publicly available and supports modification-aware basecalling, suitable public datasets for benchmarking m5C, inosine, m6A, and PseU detection on RNA004 are currently lacking. Dorado’s modification-aware models are trained on ONT’s internal data, which is not publicly released. Therefore, it is not currently feasible to evaluate or directly compare SegPore’s performance against Dorado for m5C, inosine, m6A, and PseU detection.

We would also like to emphasize that SegPore’s main contribution lies in raw signal segmentation, which is an upstream task in the RNA modification detection pipeline. To assess its performance in this context, we benchmarked SegPore against f5c and Uncalled4 on public RNA004 datasets for segmentation quality. Please refer to our response to Point 1 of Reviewer 1 for details.

Our results show that the characteristic “jiggling” behavior is also observed in RNA004 data (Supplementary Figure S4), and SegPore achieves better segmentation performance than both f5c and Uncalled4 (Table 2).

Recommendations for the authors:

Reviewing Editor:

Please note that we also received the following comments on the submission, which we encourage you to take into account:

took a look at the work and for what I saw it only mentions/uses RNA002 chemistry, which is deprecated, effectively making this software unusable by anyone any more, as RNA002 is not commercially available. While the results seem promising, the authors need to show that it would work for RNA004. Notably, there is an alternative software for resquiggling for RNA004 (not Tombo or Nanopolish, but the GPU-accelerated version of Nanopolish (f5C), which does support RNA004. Therefore, they need to show that SegPore works for RNA004, because otherwise it is pointless to see that this method works better than others if it does not support current sequencing chemistries and only works for deprecated chemistries, and people will keep using f5C because its the only one that currently works for RNA004. Alternatively, if there would be biological insights won from the method, one could justify not implementing it in RNA004, but in this case, RNA002 is deprecated since March 2024, and the paper is purely methodological.

Thank you for the comment. We agree that support for current sequencing chemistries is essential for practical utility. While SegPore was initially developed and benchmarked on RNA002 due to the availability of public data, we have now extended SegPore to support RNA004 chemistry.

To address this concern, we performed a benchmark comparison using public RNA004 datasets against tools specifically designed for RNA004, including f5c and Uncalled4. Please refer to our response to Point 1 of Reviewer 1 for details. The results show that SegPore consistently outperforms f5c and Uncalled4 in segmentation accuracy on RNA004 data.

Reviewer #2 (Recommendations for the authors):

Various statements are made throughout the text that require further explanation, which might actually be defined in more detail elsewhere sometimes but are simply hard to find in the current form.

(1) Page 2, “In this technique, five nucleotides (5mers) reside in the nanopore at a time, and each 5mer generates a characteristic current signal based on its unique sequence and chemical properties (16).”

5mer? Still on R9 or just ignoring longer range influences, relevant? It is indeed a R9.4 model from ONT.

Thank you for the observation. We apologize for the confusion and have clarified the relevant paragraph to indicate that the method is developed for RNA002 data by default. Specifically, we have added the following sentence:

“Two versions of the direct RNA sequencing (DRS) kits are available: RNA002 and RNA004. Unless otherwise specified, this study focuses on RNA002 data.”

(2) Page 3, “Employ models like Hidden Markov Models (HMM) to segment the signal, but they are prone to noise and inaccuracies.”

That's the alignment/calling part, not the segmentation?

Thank you for the comment. We apologize for the confusion. To clarify the distinction between segmentation and alignment, we added a new paragraph before the one in question to explain the general workflow of Nanopore DRS data analysis and to clearly define the task of segmentation. The added text reads:

“The general workflow of Nanopore direct RNA sequencing (DRS) data analysis is as follows. First, the raw electrical signal from a read is basecalled using tools such as Guppy or Dorado, which produce the nucleotide sequence of the RNA molecule. However, these basecalled sequences do not include the precise start and end positions of each ribonucleotide (or k-mer) in the signal. Because basecalling errors are common, the sequences are typically mapped to a reference genome or transcriptome using minimap2 to recover the correct reference sequence. Next, tools such as Nanopolish and Tombo align the raw signal to the reference sequence to determine which portion of the signal corresponds to each k-mer. We define this process as the segmentation task, referred to as "eventalign" in Nanopolish. Based on this alignment, Nanopolish extracts various features—such as the start and end positions, mean, and standard deviation of the signal segment corresponding to a k-mer. This signal segment or its derived features is referred to as an "event" in Nanopolish.”

We also revised the following paragraph describing SegPore to more clearly contrast its approach:

“In SegPore, we first segment the raw signal into small fragments using a Hierarchical Hidden Markov Model (HHMM), where each fragment corresponds to a sub-state of a k-mer. Unlike Nanopolish and Tombo, which directly align the raw signal to the reference sequence, SegPore aligns the mean values of these small fragments to the reference. After alignment, we concatenate all fragments that map to the same k-mer into a larger segment, analogous to the "eventalign" output in Nanopolish. For RNA modification estimation, we use only the mean signal value of each reconstructed event.”

We hope this revision clarifies the difference between segmentation and alignment in the context of our method and resolves the reviewer’s concern.

(3) Page 4, Figure 1, “These segments are then aligned with the 5mer list of the reference sequence fragment using a full/partial alignment algorithm, based on a 5mer parameter table. For example, 𝐴𝑗 denotes the base "A" at the j-th position on the reference.”

I think I do understand the meaning, but I do not understand the relevance of the Aj bit in the last sentence. What is it used for?

When aligning the segments (output from Step 2) to the reference sequence in Step 3, it is possible for multiple segments to align to the same k-mer. This can occur particularly when the reference contains consecutive identical bases, such as multiple adenines (A). For example, as shown in Fig. 1A, Step 3, the first two segments (μ₁ and μ₂) are aligned to the first 'A' in the reference sequence, while the third segment is aligned to the second 'A'. In this case, the reference sequence AACTGGTTTC...GTC, which contains exactly two consecutive 'A's at the start. This notation helps to disambiguate segment alignment in regions with repeated bases.

Additionally, this figure and its subscript include mapping with Guppy and Minimap2 but do not mention Nanopolish at all, while that seems an equally important step in the preprocessing (pg5). As such it is difficult to understand the role Nanopolish exactly plays. It's also not mentioned explicitly in the SegPore Workflow on pg15, perhaps it's part of step 1 there?

We thank the reviewer for pointing this out. We apologize for the confusion. As mentioned in the public response to point 3 of Reviewer 2, SegPore uses Nanopolish to identify the poly(A) tail and transcript regions from the raw signal. SegPore then performs segmentation and alignment on the transcript portion only. This step is indeed part of Step 1 in the preprocessing workflow, as described in Supplementary Note 1, Section 3.

To clarify this in the main text, we have updated the preprocessing paragraph on page 6 to explicitly describe the role of Nanopolish:

“We begin by performing basecalling on the input fast5 file using Guppy, which converts the raw signal data into ribonucleotide sequences. Next, we align the basecalled sequences to the reference genome using Minimap2, generating a mapping between the reads and the reference sequences. Nanopolish provides two independent commands: "polya" and "eventalign".
The "polya" command identifies the adapter, poly(A) tail, and transcript region in the raw signal, which we refer to as the poly(A) detection results. The raw signal segment corresponding to the poly(A) tail is used to standardize the raw signal for each read. The "eventalign" command aligns the raw signal to a reference sequence, assigning a signal segment to individual k-mers in the reference. It also computes summary statistics (e.g., mean, standard deviation) from the signal segment for each k-mer. Each k-mer together with its corresponding signal features is termed an event. These event features are then passed into downstream tools such as m6Anet and CHEUI for RNA modification detection. For full transcriptome analysis (Figure 3), we extract the aligned raw signal segment and reference sequence segment from Nanopolish's events for each read by using the first and last events as start and end points. For in vitro transcription (IVT) data with a known reference sequence (Figure 4), we extract the raw signal segment corresponding to the transcript region for each input read based on Nanopolish’s poly(A) detection results.”

Additionally, we revised the legend of Figure 1A to explicitly include Nanopolish in step 1 as follows:

“The raw current signal fragments are paired with the corresponding reference RNA sequence fragments using Nanopolish.”

(4) Page 5, “The output of Step 3 is the "eventalign," which is analogous to the output generated by the Nanopolish "eventalign" command.”

Naming the function of Nanopolish, the output file, and later on (pg9) the alignment of the newly introduced methods the exact same "eventalign" is very confusing.

Thank you for the helpful comment. We acknowledge the potential confusion caused by using the term “eventalign” in multiple contexts. To improve clarity, we now consistently use the term “events” to refer to the output of both Nanopolish and SegPore, rather than using "eventalign" as a noun. We also added the following sentence to Step 3 (page 6) to clearly define what an “event” refers to in our manuscript:

“An "event" refers to a segment of the raw signal that is aligned to a specific k-mer on a read, along with its associated features such as start and end positions, mean current, standard deviation, and other relevant statistics.”

We have revised the text throughout the manuscript accordingly to reduce ambiguity and ensure consistent terminology.

(5) Page 5, “Once aligned, we use Nanopolish's eventalign to obtain paired raw current signal segments and the corresponding fragments of the reference sequence, providing a precise association between the raw signals and the nucleotide sequence.”

I thought the new method's HHMM was supposed to output an 'eventalign' formatted file. As this is not clearly mentioned elsewhere, is this a mistake in writing? Is this workflow dependent on Nanopolish 'eventalign' function and output or not?

We apologize for the confusion. To clarify, SegPore is not dependent on Nanopolish’s eventalign function for generating the final segmentation results. As described in our response to your comment point 2 and elaborated in the revised text on page 4, SegPore uses its own HHMM-based segmentation model to divide the raw signal into small fragments, each corresponding to a sub-state of a k-mer. These fragments are then aligned to the reference sequence based on their mean current values.

As explained in the revised manuscript:

“In SegPore, we first segment the raw signal into small fragments using a Hierarchical Hidden Markov Model (HHMM), where each fragment corresponds to a sub-state of a k-mer. Unlike Nanopolish and Tombo, which directly align the raw signal to the reference sequence, SegPore aligns the mean values of these small fragments to the reference. After alignment, we concatenate all fragments that map to the same k-mer into a larger segment, analogous to the "eventalign" output in Nanopolish. For RNA modification estimation, we use only the mean signal value of each reconstructed event.”

To avoid ambiguity, we have also revised the sentence on page 5 to more clearly distinguish the roles of Nanopolish and SegPore in the workflow. The updated sentence now reads:

“Nanopolish provides two independent commands: "polya" and "eventalign".
The "polya" command identifies the adapter, poly(A) tail, and transcript region in the raw signal, which we refer to as the poly(A) detection results. The raw signal segment corresponding to the poly(A) tail is used to standardize the raw signal for each read. The "eventalign" command aligns the raw signal to a reference sequence, assigning a signal segment to individual k-mers in the reference. It also computes summary statistics (e.g., mean, standard deviation) from the signal segment for each k-mer. Each k-mer together with its corresponding signal features is termed an event. These event features are then passed into downstream tools such as m6Anet and CHEUI for RNA modification detection. For full transcriptome analysis (Figure 3), we extract the aligned raw signal segment and reference sequence segment from Nanopolish's events for each read by using the first and last events as start and end points. For in vitro transcription (IVT) data with a known reference sequence (Figure 4), we extract the raw signal segment corresponding to the transcript region for each input read based on Nanopolish’s poly(A) detection results.”

(6) Page 5, “Since the polyA tail provides a stable reference, we normalize the raw current signals across reads, ensuring that the mean and standard deviation of the polyA tail are consistent across all reads.”

Perhaps I misread this statement: I interpret it as using the PolyA tail to do the normalization, rather than using the rest of the signal to do the normalization, and that results in consistent PolyA tails across all reads.

If it's the latter, this should be clarified, and a little detail on how the normalization is done should be added, but if my first interpretation is correct:

I'm not sure if its standard deviation is consistent across reads. The (true) value spread in this section of a read should be fairly limited compared to the rest of the signal in the read, so the noise would influence the scale quite quickly, and such noise might be introduced to pores wearing down and other technical influences. Is this really better than using the non-PolyA tail part of the reads signal, using Median Absolute Deviation to scale for a first alignment round, then re-fitting the signal scaling using Theil Sen on the resulting alignments (assigned read signal vs reference expected signal), as Tombo/Nanopolish (can) do?

Additionally, this kind of normalization should have been part of the Nanopolish eventalign already, can this not be re-used? If it's done differently it may result in different distributions than the ONT kmer table obtained for the next step.

Thank you for this detailed and thoughtful comment. We apologize for the confusion. The poly(A) tail–based normalization is indeed explained in Supplementary Note 1, Section 3, but we agree that the motivation needed to be clarified in the main text.

We have now added the following sentence in the revised manuscript (before the original statement on page 5 to provide clearer context:

“Due to inherent variability between nanopores in the sequencing device, the baseline levels and standard deviations of k-mer signals can differ across reads, even for the same transcript. To standardize the signal for downstream analyses, we extract the raw current signal segments corresponding to the poly(A) tail of each read. Since the poly(A) tail provides a stable reference, we normalize the raw current signals across reads, ensuring that the mean and standard deviation of the poly(A) tail are consistent across all reads. This step is crucial for reducing…..”

We chose to use the poly(A) tail for normalization because it is sequence-invariant—i.e., all poly(A) tails consist of identical k-mers, unlike transcript sequences which vary in composition. In contrast, using the transcript region for normalization can introduce biases: for instance, reads with more diverse k-mers (having inherently broader signal distributions) would be forced to match the variance of reads with more uniform k-mers, potentially distorting the baseline across k-mers.

In our newly added RNA004 benchmark experiment, we used the default normalization provided by f5c, which does not include poly(A) tail normalization. Despite this, SegPore was still able to mask out noise and outperform both f5c and Uncalled4, demonstrating that our segmentation method is robust to different normalization strategies.

(7) Page 7, “The initialization of the 5mer parameter table is a critical step in SegPore's workflow. By leveraging ONT's established kmer models, we ensure that the initial estimates for unmodified 5mers are grounded in empirical data.”

It looks like the method uses Nanopolish for a first alignment, then improves the segmentation matching the reference sequence/expected 5mer values. I thought the Nanopolish model/tables are based on the same data, or similarly obtained. If they are different, then why the switch of kmer model? Now the original alignment may have been based on other values, and thus the alignment may seem off with the expected kmer values of this table.

Thank you for this insightful question. To clarify, SegPore uses Nanopolish only to identify the poly(A) tail and transcript regions from the raw signal. In the bulk in vivo data analysis, we use Nanopolish’s first event as the start and the last event as the end to extract the aligned raw signal chunk and its corresponding reference sequence. Since SegPore relies on Nanopolish solely to delineate the transcript region for each read, it independently aligns the raw signals to the reference sequence without refining or adjusting Nanopolish’s segmentation results.

While SegPore's 5-mer parameter table is initially seeded using ONT’s published unmodified k-mer models, we acknowledge that empirical signal values may deviate from these reference models due to run-specific technical variation and the presence of RNA modifications. For this reason, SegPore includes a parameter re-estimation step to refine the mean and standard deviation values of each k-mer based on the current dataset.

The re-estimation process consists of two layers. In the outer layer, we select a set of 5mers that exhibit both modified and unmodified states based on the GMM results (Section 6 of Supplementary Note 1), while the remaining 5mers are assumed to have only unmodified states. In the inner layer, we align the raw signals to the reference sequences using the 5mer parameter table estimated in the outer layer (Section 5 of Supplementary Note 1). Based on the alignment results, we update the 5mer parameter table in the outer layer. This two-layer process is generally repeated for 3~5 iterations until the 5mer parameter table converges.This re-estimation ensures that:

(1) The adjusted 5mer signal baselines remain close to the ONT reference (for consistency);

(2) The alignment score between the observed signal and the reference sequence is optimized (as detailed in Equation 11, Section 5 of Supplementary Note 1);

(3) Only 5mers that show a clear difference between the modified and unmodified components in the GMM are considered subject to modification.

By doing so, SegPore achieves more accurate signal alignment independent of Nanopolish’s models, and the alignment is directly tuned to the data under analysis.

(8) Page 9, “The output of the alignment algorithm is an eventalign, which pairs the base blocks with the 5mers from the reference sequence for each read (Fig. 1C).”

“Modification prediction

After obtaining the eventalign results, we estimate the modification state of each motif using the 5mer parameter table.”

This wording seems to have been introduced on page 5 but (also there) reads a bit confusingly as the name of the output format, file, and function are now named the exact same "eventalign". I assume the obtained eventalign results now refer to the output of your HHMM, and not the original Nanopolish eventalign results, based on context only, but I'd rather have a clear naming that enables more differentiation.

We apologize for the confusion. We have revised the sentence as follows for clarity:

“A detailed description of both alignment algorithms is provided in Supplementary Note 1. The output of the alignment algorithm is an alignment that pairs the base blocks with the 5mers from the reference sequence for each read (Fig. 1C). Base blocks aligned to the same 5-mer are concatenated into a single raw signal segment (referred to as an “event”), from which various features—such as start and end positions, mean current, and standard deviation—are extracted. Detailed derivation of the mean and standard deviation is provided in Section 5.3 in Supplementary Note 1. In the remainder of this paper, we refer to these resulting events as the output of eventalign analysis or the segmentation task. ”

(9) Page 9, “Since a single 5mer can be aligned with multiple base blocks, we merge all aligned base blocks by calculating a weighted mean. This weighted mean represents the single base block mean aligned with the given 5mer, allowing us to estimate the modification state for each site of a read.”

I assume the weights depend on the length of the segment but I don't think it is explicitly stated while it should be.

Thank you for the helpful observation. To improve clarity, we have moved this explanation to the last paragraph of the previous section (see response to point 8), where we describe the segmentation process in more detail.

Additionally, a complete explanation of how the weighted mean is computed is provided in Section 5.3 of Supplementary Note 1. It is derived from signal points that are assigned to a given 5mer.

(10) Page 10, “Afterward, we manually adjust the 5mer parameter table using heuristics to ensure that the modified 5mer distribution is significantly distinct from the unmodified distribution.”

Using what heuristics? If this is explained in the supplementary notes then please refer to the exact section.

Thank you for pointing this out. The heuristics used to manually adjust the 5mer parameter table are indeed explained in detail in Section 7 of Supplementary Note 1.

To clarify this in the manuscript, we have revised the sentence as follows:

“Afterward, we manually adjust the 5mer parameter table using heuristics to ensure that the modified 5mer distribution is significantly distinct from the unmodified distribution (see details in Section 7 of Supplementary Note 1).”

(11) Page 10, “Once the table is fixed, it is used for RNA modification estimation in the test data without further updates.”

By what tool/algorithm? Perhaps it is your own implementation, but with the next section going into segmentation benchmarking and using Nanopolish before this seems undefined.

Thank you for pointing this out. We use our own implementation. See Algorithm 3 in Section 6 of Supplementary Note 1.

We have revised the sentence for clarity:

“Once a stabilized 5mer parameter table is estimated from the training data, it is used for RNA modification estimation in the test data without further updates. A more detailed description of the GMM re-estimation process is provided in Section 6 of Supplementary Note 1.”

(12) Page 11, “A 5mer was considered significantly modified if its read coverage exceeded 1,500 and the distance between the means of the two Gaussian components in the GMM was greater than 5.”

Considering the scaling done before also not being very detailed in what range to expect, this cutoff doesn't provide any useful information. Is this a pA value?

Thank you for the observation. Yes, the value refers to the current difference measured in picoamperes (pA). To clarify this, we have revised the sentence in the manuscript to include the unit explicitly:

“A 5mer was considered significantly modified if its read coverage exceeded 1,500 and the distance between the means of the two Gaussian components in the GMM was greater than 5 picoamperes (pA).”

(13) Page 13, “The raw current signals, as shown in Figure 1B.”

Wrong figure? Figure 2B seems logical.

Thank you for catching this. You are correct—the reference should be to Figure 2B, not Figure 1B. We have corrected this in the revised manuscript.

(14) Page 14, Figure 2A, these figures supposedly support the jiggle hypothesis but the examples seem to match only half the explanation. Any of these jiggles seem to be followed shortly by another in the opposite direction, and the amplitude seems to match better within each such pair than the next or previous segments. Perhaps there is a better explanation still, and this behaviour can be modelled as such instead.

Thank you for your comment. We acknowledge that the observed signal patterns may appear ambiguous and could potentially suggest alternative explanations. However, as shown in Figure 2A, the red dots tend to align closely with the baseline of the previous state, while the blue dots align more closely with the baseline of the next state. We interpret this as evidence for the "jiggling" hypothesis, where k-mer temporarily oscillates between adjacent states during translocation.

That said, we agree that more sophisticated models could be explored to better capture this behavior, and we welcome suggestions or references to alternative models. We will consider this direction in future work.

(15) Page 15, “This occurs because subtle transitions within a base block may be mistaken for transitions between blocks, leading to inflated transition counts.”

Is it really a "subtle transition" if it happens within a base block? It seems this is not a transition and thus shouldn't be named as such.

Thank you for pointing this out. We agree that the term “subtle transition” may be misleading in this context. We revised the sentence to clarify the potential underlying cause of the inflated transition counts:

“This may be due to a base block actually corresponding to a sub-state of a single 5mer, rather than each base block corresponding to a full 5mer, leading to inflated transition counts. To address this issue, SegPore’s alignment algorithm was refined to merge multiple base blocks (which may represent sub-states of the same 5mer) into a single 5mer, thereby facilitating further analysis.”

(16) Page 15, “The SegPore "eventalign" output is similar to Nanopolish's "eventalign" command.”

To the output of that command, I presume, not to the command itself.

Thank you for pointing out the ambiguity. We have revised the sentence for clarity:

“The final outputs of SegPore are the events and modification state predictions. SegPore’s events are similar to the outputs of Nanopolish’s "eventalign" command, in that they pair raw current signal segments with the corresponding RNA reference 5-mers. Each 5-mer is associated with various features — such as start and end positions, mean current, and standard deviation — derived from the paired signal segment.”

(17) Page 15, “For selected 5mers, SegPore also provides the modification rate for each site and the modification state of that site on individual reads.”

What selection? Just all kmers with a possible modified base or a more specific subset?

We revised the sentence to clarify the selection criteria:

“For selected 5mers that exhibit both a clearly unmodified and a clearly modified signal component, SegPore reports the modification rate at each site, as well as the modification state of that site on individual reads.”

(18) Page 16, “A key component of SegPore is the 5mer parameter table, which specifies the mean and standard deviation for each 5mer in both modified and unmodified states (Figure 2A).”

Wrong figure?

Thank you for pointing this out. You are correct—it should be Figure 1A, not Figure 2A. We intended to visually illustrate the structure of the 5mer parameter table in Figure 1A, and we have corrected this reference in the revised manuscript.

(19) Page 16, Table 1, I can't quite tell but I assume this is based on all kmers in the table, not just a m6A modified subset. A short added statement to make this clearer would help.

Yes, you are right—it is averaged over all 5mers. We have revised the sentence for clarity as follows:

" As shown in Table 1, SegPore consistently achieved the best performance averaged on all 5mers across all datasets..…."

(20) Page 16, “Since the peaks (representing modified and unmodified states) are separable for only a subset of 5mers, SegPore can provide modification parameters for these specific 5mers. For other 5mers, modification state predictions are unavailable.”

Can this be improved using some heuristics rather than the 'distance of 5' cutoff as described before? How small or big is this subset, compared to how many there should be to cover all cases?

We agree that more sophisticated strategies could potentially improve performance. In this study, we adopted a relatively conservative approach to minimize false positives by using a heuristic cutoff of 5 picoamperes. This value was selected empirically and we did not explore alternative cutoffs. Future work could investigate more refined or data-driven thresholding strategies.

(21) Page 16, “Tombo used the "resquiggle" method to segment the raw signals, and we standardized the segments using the polyA tail to ensure a fair comparison.”

I don't know what or how something is "standardized" here.

Standardized’ refers to the poly(A) tail–based signal normalization described in our response to point 6. We applied this normalization to Tombo’s output to ensure a fair comparison across methods. Without this standardization, Tombo’s performance was notably worse. We revised the sentence as follows:

“Tombo used the "resquiggle" method to segment the raw signals, and we standardized the segments using the poly(A) tail to ensure a fair comparison (See preprocessing section in Materials and Methods).”

(22) Page 16, “To benchmark segmentation performance, we used two key metrics: (1) the log-likelihood of the segment mean, which measures how closely the segment matches ONT's 5mer parameter table (used as ground truth), and (2) the standard deviation (std) of the segment, where a lower std indicates reduced noise and better segmentation quality. If the raw signal segment aligns correctly with the corresponding 5mer, its mean should closely match ONT's reference, yielding a high log-likelihood. A lower std of the segment reflects less noise and better performance overall.”

Here the segmentation part becomes a bit odd:

A: Low std can be/is achieved by dropping any noisy bits, making segments really small (partly what happens here with the transition segments). This may be 'true' here, in the sense that the transition is not really part of the segment, but the comparison table is a bit meaningless as the other tools forcibly assign all data to kmers, instead of ignoring parts as transition states. In other words, it is a benchmark that is easy to cheat by assigning more data to noise/transition states.

B: The values shown are influenced by the alignment made between the read and expected reference signal. Especially Tombo tends to forcibly assign data to whatever looks the most similar nearby rather than providing the correct alignment. So the "benchmark of the segmentation performance" is more of an "overall benchmark of the raw signal alignment". Which is still a good, useful thing, but the text seems to suggest something else.

Thank you for raising these important concerns regarding the segmentation benchmarking.

Regarding point A, the base blocks aligned to the same 5mer are concatenated into a single segment, including the short transition blocks between them. These transition blocks are typically very short (4~10 signal points, average 6 points), while a typical 5mer segment contains around 20~60 signal points. To assess whether SegPore’s performance is inflated by excluding transition segments, we conducted an additional comparison: we removed 6 boundary signal points (3 from the start and 3 from the end) from each 5mer segment in Nanopolish and Tombo’s results to reduce potential noise. The new comparison table is shown in the following:

SegPore consistently demonstrates superior performance. Its key contribution lies in its ability to recognize structured noise in the raw signal and to derive more accurate mean and standard deviation values that more faithfully represent the true state of the k-mer in the pore. The improved mean estimates are evidenced by the clearly separated peaks of modified and unmodified 5mers in Figures 3A and 4B, while the improved standard deviation is reflected in the segmentation benchmark experiments.

Regarding point B, we apologize for the confusion. We have added a new paragraph to the introduction to clarify that the segmentation task indeed includes the alignment step.

“The general workflow of Nanopore direct RNA sequencing (DRS) data analysis is as follows. First, the raw electrical signal from a read is basecalled using tools such as Guppy or Dorado, which produce the nucleotide sequence of the RNA molecule. However, these basecalled sequences do not include the precise start and end positions of each ribonucleotide (or k-mer) in the signal. Because basecalling errors are common, the sequences are typically mapped to a reference genome or transcriptome using minimap2 to recover the correct reference sequence. Next, tools such as Nanopolish and Tombo align the raw signal to the reference sequence to determine which portion of the signal corresponds to each k-mer. We define this process as the segmentation task, referred to as "eventalign" in Nanopolish. Based on this alignment, Nanopolish extracts various features—such as the start and end positions, mean, and standard deviation of the signal segment corresponding to a k-mer. This signal segment or its derived features is referred to as an "event" in Nanopolish. The resulting events serve as input for downstream RNA modification detection tools such as m6Anet and CHEUI.”

(23) Page 17 “Given the comparable methods and input data requirements, we benchmarked SegPore against several baseline tools, including Tombo, MINES (26), Nanom6A (27), m6Anet, Epinano (28), and CHEUI (29).”

It seems m6Anet is actually Nanopolish+m6Anet in Figure 3C, this needs a minor clarification here.

m6Anet uses Nanopolish’s estimated events as input by default.

(24) Page 18, Figure 3, A and B are figures without any indication of what is on the axis and from the text I believe the position next to each other on the x-axis rather than overlapping is meaningless, while their spread is relevant, as we're looking at the distribution of raw values for this 5mer. The figure as is is rather confusing.

Thanks for pointing out the confusion. We have added concrete values to the axes in Figures 3A and 3B and revised the figure legend as follows in the manuscript:

“(A) Histogram of the estimated mean from current signals mapped to an example m6A-modified genomic location (chr10:128548315, GGACT) across all reads in the training data, comparing Nanopolish (left) and SegPore (right). The x-axis represents current in picoamperes (pA).

(B) Histogram of the estimated mean from current signals mapped to the GGACT motif at all annotated m6A-modified genomic locations in the training data, again comparing Nanopolish (left) and SegPore (right). The x-axis represents current in picoamperes (pA).”

(25) Page 18 “SegPore's results show a more pronounced bimodal distribution in the raw signal segment mean, indicating clearer separation of modified and unmodified signals.”

Without knowing the correct values around the target kmer (like Figure 4B), just the more defined bimodal distribution could also indicate the (wrongful) assignment of neighbouring kmer values to this kmer instead, hence this statement lacks some needed support, this is just one interpretation of the possible reasons.

Thank you for the comment. We have added concrete values to Figures 3A and 3B to support this point. Both peaks fall within a reasonable range: the unmodified peak (125 pA) is approximately 1.17 pA away from its reference value of 123.83 pA, and the modified peak (118 pA) is around 7 pA away from the unmodified peak. This shift is consistent with expected signal changes due to RNA modifications (usually less than 10 pA), and the magnitude of the difference suggests that the observed bimodality is more likely caused by true modification events rather than misalignment.

(26) Page 18 “Furthermore, when pooling all reads mapped to m6A-modified locations at the GGACT motif, SegPore showed prominent peaks (Fig. 3B), suggesting reduced noise and improved modification detection.”

I don't think the prominent peaks directly suggest improved detection, this statement is a tad overreaching.

We revised the sentense to the following:

“SegPore exhibited more distinct peaks (Fig. 3B), indicating reduced noise and potentially enabling more reliable modification detection”.

(27) Page18 “(2) direct m6A predictions from SegPore's Gaussian Mixture Model (GMM), which is limited to the six selected 5mers.”

The 'six selected' refers to what exactly? Also, 'why' this is limited to them is also unclear as it is, and it probably would become clearer if it is clearly defined what this refers to.

It is explained the page 16 in the SegPore’s workflow in the original manuscript as follows:

“A key component of SegPore is the 5mer parameter table, which specifies the mean and standard deviation for each 5mer in both modified and unmodified states (Fig. 2A1A). Since the peaks (representing modified and unmodified states) are separable for only a subset of 5mers, SegPore can provide modification parameters for these specific 5mers. For other 5mers, modification state predictions are unavailable.”

e select a small set of 5mers that show clear peaks (modified and unmodified 5mers) in GMM in the m6A site-level data analysis. These 5mers are provided in Supplementary Fig. S2C, as explained in the section “m6A site level benchmark” in the Material and Methods (page 12 in the original manuscript).

“…transcript locations into genomic coordinates. It is important to note that the 5mer parameter table was not re-estimated for the test data. Instead, modification states for each read were directly estimated using the fixed 5mer parameter table. Due to the differences between human (Supplementary Fig. S2A) and mouse (Supplementary Fig. S2B), only six 5mers were found to have m6A annotations in the test data’s ground truth (Supplementary Fig. S2C). For a genomic location to be identified as a true m6A modification site, it had to correspond to one of these six common 5mers and have a read coverage of greater than 20. SegPore derived the ROC and PR curves for benchmarking based on the modification rate at each genomic location….”

We have updated the sentence as follows to increase clarity:

“which is limited to the six selected 5mers that exhibit clearly separable modified and unmodified components in the GMM (see Materials and Methods for details).”

(28) Page 19, Figure 4C, the blue 'Unmapped' needs further explanation. If this means the segmentation+alignment resulted in simply not assigning any segment to a kmer, this would indicate issues in the resulting mapping between raw data and kmers as the data that probably belonged to this kmer is likely mapped to a neighbouring kmer, possibly introducing a bimodal distribution there.

This is due to deletion event in the full alignment algorithm. See Page 8 of SupplementaryNote1:

During the traceback step of the dynamic programming matrix, not every 5mer in the reference sequence is assigned a corresponding raw signal fragment—particularly when the signal’s mean deviates substantially from the expected mean of that 5mer. In such cases, the algorithm considers the segment to be generated by an unknown 5mer, and the corresponding reference 5mer is marked as unmapped.

(29) Page 19, “For six selected m6A motifs, SegPore achieved an ROC AUC of 82.7% and a PR AUC of 38.7%, earning the third-best performance compared with deep leaning methods m6Anet and CHEUI (Fig. 3D).”

How was this selection of motifs made, are these related to the six 5mers in the middle of Supplementary Figure S2? Are these the same six as on page 18? This is not clear to me.

It is the same, see the response to point 27.

(30) Page 21 “Biclustering reveals that modifications at the 6th, 7th, and 8th genomic locations are specific to certain clusters of reads (clusters 4, 5, and 6), while the first five genomic locations show similar modification patterns across all reads.”

This reads rather confusingly. Both the '6th, 7th, and 8th genomic locations' and 'clusters 4,5,6' should be referred to in clearer terms. Either mark them in the figure as such or name them in the text by something that directly matches the text in the figure.

We have added labels to the clusters and genomic locations Figure 4C, and revised the sentence as follows:

“Biclustering reveals that modifications at g6 are specific to cluster C4, g7 to cluster C5, and g8 to cluster C6, while the first five genomic locations (g1 to g5) show similar modification patterns across all reads.”

(31) Page 21, “We developed a segmentation algorithm that leverages the jiggling property in the physical process of DRS, resulting in cleaner current signals for m6A identification at both the site and single-molecule levels.”

Leverages, or just 'takes into account'?

We designed our HHMM specifically based on the jiggling hypothesis, so we believe that using the term “leverage” is appropriate.

(32) Page 21, “Our results show that m6Anet achieves superior performance, driven by SegPore's enhanced segmentation.”

Superior in what way? It barely improves over Nanopolish in Figure 3C and is outperformed by other methods in Figure 3D. The segmentation may have improved but this statement says something is 'superior' driven by that 'enhanced segmentation', so that cannot refer to the segmentation itself.

We revise it as follows in the revised manuscript:

”Our results demonstrate that SegPore’s segmentation enables clear differentiation between m6A-modified and unmodified adenosines.”

(33) Page 21, “In SegPore, we assume a drastic change between two consecutive 5mers, which may hold for 5mers with large difference in their current baselines but may not hold for those with small difference.”

The implications of this assumption don't seem highlighted enough in the work itself and may be cause for falsely discovering bi-modal distributions. What happens if such a 5mer isn't properly split, is there no recovery algorithm later on to resolve these cases?

We agree that there is a risk of misalignment, which can result in a falsely observed bimodal distribution. This is a known and largely unavoidable issue across all methods, including deep neural network–based methods. For example, many of these models rely on a CTC (Connectionist Temporal Classification) layer, which implicitly performs alignment and may also suffer from similar issues.

Misalignment is more likely when the current baselines of neighboring k-mers are close. In such cases, the model may struggle to confidently distinguish between adjacent k-mers, increasing the chance that signals from neighboring k-mers are incorrectly assigned. Accurate baseline estimation for each k-mer is therefore critical—when baselines are accurate, the correct alignment typically corresponds to the maximum likelihood.

We have added the following sentence to the discussion to acknowledge this limitation:

“As with other RNA modification estimation methods, SegPore can be affected by misalignment errors, particularly when the baseline signals of adjacent k-mers are similar. These cases may lead to spurious bimodal signal distributions and require careful interpretation.”

(34) Page 21, “Currently, SegPore models only the modification state of the central nucleotide within the 5mer. However, modifications at other positions may also affect the signal, as shown in Figure 4B. Therefore, introducing multiple states to the 5mer could help to improve the performance of the model.”

The meaning of this statement is unclear to me. Is SegPore unable to combine the information of overlapping kmers around a possibly modified base (central nucleotide), or is this referring to having multiple possible modifications in a single kmer (multiple states)?

We mean there can be modifications at multiple positions of a single 5mer, e.g. C m5C m6A m7G T. We have revised the sentence to:

“Therefore, introducing multiple states for a 5mer to accout for modifications at mutliple positions within the same 5mer could help to improve the performance of the model.”

(35) Page 22, “This causes a problem when apply DNN-based methods to new dataset without short read sequencing-based ground truth. Human could not confidently judge if a predicted m6A modification is a real m6A modification.”

Grammatical errors in both these sentences. For the 'Human could not' part, is this referring to a single person's attempt or more extensively tested?

Thanks for the comment. We have revised the sentence as follows:

“This poses a challenge when applying DNN-based methods to new datasets without short-read sequencing-based ground truth. In such cases, it is difficult for researchers to confidently determine whether a predicted m6A modification is genuine (see Supplmentary Figure S5).”

(36) Page 22, “…which is easier for human to interpret if a predicted m6A site is real.”

"a" human, but also this probably meant to say 'whether' instead of 'if', or 'makes it easier'.

Thanks for the advice. We have revise the sentence as follows:

“One can generally observe a clear difference in the intensity levels between 5mers with an m6A and those with a normal adenosine, which makes it easier for a researcher to interpret whether a predicted m6A site is genuine.”

(37) Page 22, “…and noise reduction through its GMM-based approach…”

Is the GMM providing noise reduction or segmentation?

Yes, we agree that it is not relevant. We have removed the sentence in the revised manuscript as follows:

“Although SegPore provides clear interpretability and noise reduction through its GMM-based approach, there is potential to explore DNN-based models that can directly leverage SegPore's segmentation results.”

(38) Page 23, “SegPore effectively reduces noise in the raw signal, leading to improved m6A identification at both site and single-molecule levels…”

Without further explanation in what sense this is meant, 'reduces noise' seems to overreach the abilities, and looks more like 'masking out'.

Following the reviewer’s suggestion, we change it to ‘mask out'’ in the revised manuscript.

“SegPore effectively masks out noise in the raw signal, leading to improved m6A identification at both site and single-molecule levels.”

Reviewer #3 (Recommendations for the authors):

I recommend the publication of this manuscript, provided that the following comments (and the comments above) are addressed.

In general, the authors state that SegPore represents an improvement on existing software. These statements are largely unquantified, which erodes their credibility. I have specified several of these in the Minor comments section.

Page 5, Preprocessing: The authors comment that the poly(A) tail provides a stable reference that is crucial for the normalisation of all reads. How would this step handle reads that have variable poly(A) tail lengths? Or have interrupted poly(A) tails (e.g. in the case of mRNA vaccines that employ a linker sequence)?

We apologize for the confusion. The poly(A) tail–based normalization is explained in Supplementary Note 1, Section 3.

As shown in Author response image 1 below, the poly(A) tail produces a characteristic signal pattern—a relatively flat, squiggly horizontal line. Due to variability between nanopores, raw current signals often exhibit baseline shifts and scaling of standard deviations. This means that the signal may be shifted up or down along the y-axis and stretched or compressed in scale.

Author response image 1.

The normalization remains robust with variable poly(A) tail lengths, as long as the poly(A) region is sufficiently long. The linker sequence will be assigned to the adapter part rather than the poly(A) part.

To improve clarity in the revised manuscript, we have added the following explanation:

“Due to inherent variability between nanopores in the sequencing device, the baseline levels and standard deviations of k-mer signals can differ across reads, even for the same transcript. To standardize the signal for downstream analyses, we extract the raw current signal segments corresponding to the poly(A) tail of each read. Since the poly(A) tail provides a stable reference, we normalize the raw current signals across reads, ensuring that the mean and standard deviation of the poly(A) tail are consistent across all reads. This step is crucial for reducing…..”

We chose to use the poly(A) tail for normalization because it is sequence-invariant—i.e., all poly(A) tails consist of identical k-mers, unlike transcript sequences which vary in composition. In contrast, using the transcript region for normalization can introduce biases: for instance, reads with more diverse k-mers (having inherently broader signal distributions) would be forced to match the variance of reads with more uniform k-mers, potentially distorting the baseline across k-mers.

Page 7, 5mer parameter table: r9.4_180mv_70bps_5mer_RNA is an older kmer model (>2 years). How does your method perform with the newer RNA kmer models that do permit the detection of multiple ribonucleotide modifications? Addressing this comment is crucial because it is feasible that SegPore will underperform in comparison to the newer RNA base caller models (requiring the use of RNA004 datasets).

Thank you for highlighting this important point. For RNA004, we have updated SegPore to ensure compatibility with the latest kit. In our revised manuscript, we demonstrate that the translocation-based segmentation hypothesis remains valid for RNA004, as supported by new analyses presented in the supplementary Figure S4.

Additionally, we performed a new benchmark with f5c and Uncalled4 in RNA004 data in the revised manuscript (Table 2), where SegPore exhibit a better performance than f5c and Uncalled4.

We agree that benchmarking against the latest Dorado models—specifically rna004_130bps_hac@v5.1.0 and rna004_130bps_sup@v5.1.0, which include built-in modification detection capabilities—would provide valuable context for evaluating the utility of SegPore. However, generating a comprehensive k-mer parameter table for RNA004 requires a large, well-characterized dataset. At present, such data are limited in the public domain. Additionally, Dorado is developed by ONT and its internal training data have not been released, making direct comparisons difficult.

Our current focus is on improving raw signal segmentation quality, which are upstream tasks critical to many downstream analyses, including RNA modification detection. Future work may include benchmarking SegPore against models like Dorado once appropriate data become available.

The Methods and Results sections contain redundant information - please streamline the information in these sections and reduce the redundancy. For example, the benchmarking section may be better situated in the Results section.

Following your advice, we have removed redundant texts about the Segmentation benchmark from Materials and Methods in the revised manuscript.

Minor comments

(1) Introduction

Page 3: "By incorporating these dynamics into its segmentation algorithm...". Please provide an example of how motor protein dynamics can impact RNA translocation. In particular, please elaborate on why motor protein dynamics would impact the translocation of modified ribonucleotides differently to canonical ribonucleotides. This is provided in the results, but please also include details in the Introduction.

Following your advice, we added one sentence to explain how the motor protein affect the translocation of the DNA/RNA molecule in the revised manuscript.

“This observation is also supported by previous reports, in which the helicase (the motor protein) translocates the DNA strand through the nanopore in a back-and-forth manner. Depending on ATP or ADP binding, the motor protein may translocate the DNA/RNA forward or backward by 0.5-1 nucleotides.”

As far as we understand, this translocation mechanism is not specific to modified or unmodified nucleotides. For further details, we refer the reviewer to the original studies cited.

Page 3: "This lack of interpretability can be problematic when applying these methods to new datasets, as researchers may struggle to trust the predictions without a clear understanding of how the results were generated." Please provide details and citations as to why researchers would struggle to trust the predictions of m6Anet. Is it due to a lack of understanding of how the method works, or an empirically demonstrated lack of reliability?

Thank you for pointing this out. The lack of interpretability in deep learning models such as m6Anet stems primarily from their “black-box” nature—they provide binary predictions (modified or unmodified) without offering clear reasoning or evidence for each call.

When we examined the corresponding raw signals, we found it difficult to visually distinguish whether a signal segment originated from a modified or unmodified ribonucleotide. The difference is often too subtle to be judged reliably by a human observer. This is illustrated in the newly added Supplementary Figure S5, which shows Nanopolish-aligned raw signals for the central 5mer GGACT in Figure 4B, displayed both uncolored and colored by modification state (according to the ground truth).

Although deep neural networks can learn subtle, high-dimensional patterns in the signal that may not be readily interpretable, this opacity makes it difficult for researchers to trust the predictions—especially in new datasets where no ground truth is available. The issue is not necessarily an empirically demonstrated lack of reliability, but rather a lack of transparency and interpretability.

We have updated the manuscript accordingly and included Supplementary Figure S5 to illustrate the difficulty in interpreting signal differences between modified and unmodified states.

Page 3: "Instead of relying on complex, opaque features...". Please provide evidence that the research community finds the figures generated by m6Anet to be difficult to interpret, or delete the sections relating to its perceived lack of usability.

See the figure provided in the response to the previous point. We added a reference to this figure in the revised manuscript.

“Instead of relying on complex, opaque features (see Supplementary Figure S5), SegPore leverages baseline current levels to distinguish between…..”

(2) Materials and Methods

Page 5, Preprocessing: "We begin by performing basecalling on the input fast5 file using Guppy, which converts the raw signal data into base sequences.". Please change "base" to ribonucleotide.

Revised as requested.

Page 5 and throughout, please refer to poly(A) tail, rather than polyA tail throughout.

Revised as requested.

Page 5, Signal segmentation via hierarchical Hidden Markov model: "...providing more precise estimates of the mean and variance for each base block, which are crucial for downstream analyses such as RNA modification prediction." Please specify which method your HHMM method improves upon.

Thank you for the suggestion. Since this section does not include a direct comparison, we revised the sentence to avoid unsupported claims. The updated sentence now reads:

"...providing more precise estimates of the mean and variance for each base block, which are crucial for downstream analyses such as RNA modification prediction."

Page 10, GMM for 5mer parameter table re-estimation: "Typically, the process is repeated three to five times until the 5mer parameter table stabilizes." How is the stabilisation of the 5mer parameter table quantified? What is a reasonable cut-off that would demonstrate adequate stabilisation of the 5mer parameter table?

Thank you for the comment. We assess the stabilization of the 5mer parameter table by monitoring the change in baseline values across iterations. If the absolute change in baseline values for all 5mers is less than 1e-5 between two consecutive iterations, we consider the estimation to have stabilized.

Page 11, M6A site level benchmark: why were these datasets selected? Specifically, why compare human and mouse ribonuclotide modification profiles? Please provide a justification and a brief description of the experiments that these data were derived from, and why they are appropriate for benchmarking SegPore.

Thank you for the comment. These data are taken from a previous benchmark studie about m6A estimation from RNA002 data in the literature (https://doi.org/10.1038/s41467-023-37596-5). We think the data are appropreciate here.

Thank you for the comment. The datasets used were taken from a previous benchmark study on m6A estimation using RNA002 data (https://doi.org/10.1038/s41467-023-37596-5). These datasets include human and mouse transcriptomes and have been widely used to evaluate the performance of RNA modification detection tools. We selected them because (i) they are based on RNA002 chemistry, which matches the primary focus of our study, and (ii) they provide a well-characterized and consistent benchmark for assessing m6A detection performance. Therefore, we believe they are appropriate for validating SegPore.

(3) Results

Page 13, RNA translocation hypothesis: "The raw current signals, as shown in Fig. 1B...". Please check/correct figure reference - Figure 1B does not show raw current signals.

Thank you for pointing this out. The correct reference should be Figure 2B. We have updated the figure citation accordingly in the revised manuscript.

Page 19, m6A identification at the site level: "For six selected m6A motifs, SegPore achieved an ROC AUC of 82.7% and a PR AUC of 38.7%, earning the third best performance compared with deep leaning methods m6Anet and CHEUI (Fig. 3D)." SegPore performs third best of all deep learning methods. Do the authors recommend its use in conjunction with m6Anet for m6A detection? Please clarify in the text.

This sentence aims to convey that SegPore alone can already achieve good performance. If interpretability is the primary goal, we recommend using SegPore on its own. However, if the objective is to identify more potential m6A sites, we suggest using the combined approach of SegPore and m6Anet. That said, we have chosen not to make explicit recommendations in the main text to avoid oversimplifying the decision or potentially misleading readers.

Page 19, m6A identification at the single molecule level: "one transcribed with m6A and the other with normal adenosine". I assume that this should be adenine? Please replace adenosine with adenine throughout.

Thank you for pointing this out. We have revised the sentence to use "adenine" where appropriate. In other instances, we retain "adenosine" when referring specifically to adenine bound to a ribose sugar, which we believe is suitable in those contexts.

Page 19, m6A identification at the single molecule level: "We used 60% of the data for training and 40% for testing". How many reads were used for training and how many for testing? Please comment on why these are appropriate sizes for training and testing datasets.

In total, there are 1.9 million reads, with 1.14 million used for training and 0.76 million  for testing (60% and 40%, respectively). We chose this split to ensure that the training set is sufficiently large to reliably estimate model parameters, while the test set remains substantial enough to robustly evaluate model performance. Although the ratio was selected somewhat arbitrarily, it balances the need for effective training with rigorous validation.

(4) Discussion

Page 21: "We believe that the de-noised current signals will be beneficial for other downstream tasks." Which tasks? Please list an example.

We have revised the text for clarity as follows:

“We believe that the de-noised current signals will be beneficial for other downstream tasks, such as the estimation of m5C, pseudouridine, and other RNA modifications.”

Page 22: "One can generally observe a clear difference in the intensity levels between 5mers with a m6A and normal adenosine, which is easier for human to interpret if a predicted m6A site is real." This statement is vague and requires qualification. Please reference a study that demonstrates the human ability to interpret two similar graphs, and demonstrate how it relates to the differences observed in your data.

We apologize for the confusion. We have revised the sentence as follows:

“One can generally observe a clear difference in the intensity levels between 5mers with an m6A and those with a normal adenosine, which makes it easier for a researcher to interpret whether a predicted m6A site is genuine.”

We believe that Figures 3A, 3B, and 4B effectively illustrate this concept.

Page 23: How long does SegPore take for its analyses compared to other similar tools? How long would it take to analyse a typical dataset?

We have added run-time statistics for datasets of varying sizes in the revised manuscript (see Supplementary Figure S6). This figure illustrates SegPore’s performance across different data volumes to help estimate typical processing times.

(5) Figures

Figure 4C. Please number the hierachical clusters and genomic locations in this figure. They are referenced in the text.

Following your suggestion, we have labeled the hierarchical clusters and genomic locations in Figure 4C in the revised manuscript.

In addition, we revised the corresponding sentence in the main text as follows: “Biclustering reveals that modifications at g6 are specific to cluster C4, g7 to cluster C5, and g8 to cluster C6, while the first five genomic locations (g1 to g5) show similar modification patterns across all reads.”

Author response:

The following is the authors’ response to the original reviews

Recommendations for the Authors:

Reviewer #1:

We think that this manuscript brings an important contribution that will be of interest in the areas of statistical physicists, (microbiota) ecology, and (biological) data science. The evidence of their results is solid and the work improves the state-of-the-art in terms of methods. We have a few concerns that, in our opinion, the authors should address.

Major concerns:

(1) While the paper could be of interest for the broad audience of e-Life, the way it is written is accessible mainly to physicists. We encourage the authors to take the broad audience into account by i) explaining better the essence of what is being done at each step, ii) highlighting the relevance of the method compared to other methods, iii) discussing the ecological implications of the results.

Examples on how to approach i) include: Modify or expand Figure 1 so that non-familiar readers can understand the summary of the work (e.g. with cartoons representing communities, diseased states and bacterial interactions and their relationship with the inference method); in each section, summarize at the beginning the purpose of what is going to be addressed in this section, and summarize at the end what the section has achieved; in Figure 2, replace symbols by their meaning as much as possible-the same for Figure 1, at the very least in the figure caption.

Example on how to approach ii): Since the authors aim to establish a bridge between disordered systems and microbiome ecology, it could be useful to expand a bit the introduction on disordered systems for biologists/biophysicists. This could be done with an additional text box, which could also highlight the advantages of this approach in comparison to other techniques (e.g. model-free approaches can also classify healthy and diseased states).

Example on how to approach iii): The authors could discuss with more depth the ecological implications of their results. For example, do they have a hypothesis on why demographic and neutral effects could dominate in healthy patients?

We thank the reviewer for the observations. Following the suggestion in the revised version, each section outlines the goal of what will be addressed in that section, and summarizes what we have achieved at the end; We also updated Figure 1 and Figure 2.

(i) For figure 1, we expanded and hopefully made more clear how we conceptualize the problem, use the data, andestablish our method. In Figure 2, we enriched the y labels of each panel with the name associated with the order parameter.

(ii) We thank the reviewer for helping us improve the readability of the introductory part, thus providing moreinsights into disordered systems techniques for a broader audience. We have added a few explanations at the end of page 2 – to explain the advantages of such methodology compared to other strategies and models.

(iii) We thank the reviewer for raising the need for a more in-depth ecological discussion of our results. A simple wayto understand why neutral effects may dominate in healthy patients is the following. Neutrality implies that species differences are mainly shaped by stochastic processes such as demographic noise, with species treated as different realizations of the same underlying stochastic ecological dynamics. In our analysis, we observe that healthy individuals tend to exhibit highly similar microbial communities, suggesting that the compositional variability among their microbiomes is compatible—at least in part—with the fluctuations expected from demographic stochasticity alone. In contrast, patients with the disease display significantly more heterogeneous microbial compositions. The diversity and structure of their gut communities cannot be satisfactorily explained by neutral demographic fluctuations alone.

This discrepancy implies that additional deterministic forces—such as altered ecological interactions—are driving the divergence observed in dysbiotic states. In diseased individuals, the breakdown of such interactions leads to a structurally distinct regime that may correspond to a phase of marginal stability, as indicated by our theoretical modeling. This shift marks a transition from a community governed by neutrality and demographic noise to one dominated by non-neutral ecological forces (as depicted in Figure 4). We added these comments in the discussion section of the revised manuscript.

(2) Taking into account the broader audience, we invite the authors to edit the abstract, as it seems to jump from one ecological concept to another without explicitly communicating what is the link between these concepts. From the first two sentences, the motivation seems to be species diversity, but no mention of diversity comes after the second sentence. There is no proper introduction/definition of what macroecological states are. After that, the authors switch to healthy and unhealthy states, without previously introducing any link between gut microbiota states and the host’s health (which perhaps could be good in the first or second sentence, although other framings can be as valid). After that, interactions appear in the text and are related to instability, but the reader might not know whether this is surprising or if healthy/unhealthy states are generally related to stability.

We pointed out a few examples, but the authors could extend their revision on i), ii) and iii) beyond such specific comments. In our opinion, this would really benefit the paper.

In response to the reviewer’s concern about conceptual clarity and structure, we substantially revised the abstract to improve its accessibility and logical flow. In the revised abstract, we now clearly link species diversity to microbiome structure and function from the outset, addressing initial confusion. We provide a concise definition of ”macroecological states,” framing them as reproducible statistical patterns reflecting community-level properties. Additionally, the revised version explicitly connects gut microbiome states to host health earlier, resolving the previous abrupt shift in focus. Finally, we conclude by highlighting how disordered systems theory advances our understanding of microbiome stability and functioning, reinforcing the novelty and broader significance of our approach. Overall, the revised abstract better serves a broad interdisciplinary audience, including readers unfamiliar with the technicalities of disordered systems or microbial ecology, while preserving the scientific depth and accuracy of our work

(3) The connection with consumer-resource (CR) models is quite unusual. In Equation (12), why do the authors assume that the consumption term does not depend on R? This should be addressed, since this term is usually dependent on R in microbial ecology models.

In case this is helpful, it is known that the symmetric Lotka-Volterra model emerges from time-scale separation in the MacArthur model, where resources reproduce logistically and are consumed by other species (e.g., plants eaten by herbivores). Consumer-resource models form a broad category, while the MacArthur model is a specific case featuring logistic resource growth. For microbes, a more meaningful justification of the generalized Lotka-Volterra (GLV) model from a consumer-resource perspective involves the consumer-resource dynamics in a chemostat, where time-scale separation is assumed and higher-order interactions are neglected. See, for example: a) The classic paper by MacArthur: R. MacArthur. Species packing and competitive equilibrium for many species. Theoretical Population Biology, 1(1):1-11, 1970. b) Recent works on time-scale separation in chemostat consumer-resource models: Anna Posfai et al., PRL, 2017 Sireci et al., PNAS, 2023 Akshit Goyal et al., PRX-Life, 2025

We thank the reviewer for the observation. We apologize for the typo that appeared in the main text and that we promptly corrected. The Consumers-Resources model we had in mind is the classical case proposed by MacArthur, where resources are self-regulated according to a logistic growth mechanism, which leads to the generalized LotkaVolterra model we employ in our work.

Minor concerns:

(1) The title has a nice pun for statistical physicists, but we wonder if it can be a bit confusing for the broader audience of e-Life. Although we leave this to the author’s decision, we’d recommend considering changing the title, making it more explicit in communicating the main contribution/result of the work.

Following the reviewer’s suggestion, we have introduced an explanatory subtitle: “Linking Species Interactions to Dysbiosis through a Disordered Lotka-Volterra Framework”.

(2) Review the references - some preprints might have already been published: Pasqualini J. 2023, Sireci 2022, Wu 2021.

We thank the reviewer for pointing our attention to this inaccuracy. We updated the references to Pasqualini and Sireci papers. To our knowledge, Wu’s paper has appeared as an arXiv preprint only.

(3) Species do not generally exhibit identical carrying capacities (see Grilli, Nat. Commun., 2020; some taxa are generally more abundant than others. The authors could discuss whether the model, with the inferred parameters, can accurately reproduce the distribution of species’ mean abundances.

We thank the reviewer for this insightful comment. As discussed in the revised manuscript (lines 294–299), our current model does not accurately reproduce the empirical species abundance distribution (SAD). This limitation stems from the assumption of constant carrying capacities across species. While empirical observations (e.g., Grilli et al., Nat. Commun., 2020 [1]) show heterogeneous mean abundances often following power-law or log-normal distributions. However, our model assumes constant carrying capacity, resulting in SADs devoid of fat tails, which diverge from empirical data.

This simplification is implemented to maintain the analytical tractability of the disordered generalized Lotka-Volterra (dGLV) framework, a common approach also found in prior works such as Bunin (2017) and Barbier et al. (2018) [2, 3]. Introducing heterogeneity in carrying capacities, such as drawing them from a log-normal distribution, or switching to multiplicative (rather than demographic) noise, could indeed produce SADs that better align with empirical data. Nevertheless, implementing changes would significantly complicate the analytical treatment.

We acknowledge these directions as promising avenues for future research. They could help enhance the empirical realism of the model and its capacity to capture observed macroecological patterns while posing new theoretical challenges for disordered systems analysis

(4) A substantial number of cited works (Grilli, Nat. Commun., 2020; Zaoli & Grilli, Science Advances, 2021; Sireci et al., PNAS, 2023; Po-Yi Ho et al., eLife, 2022) suggest that environmental fluctuations play a crucial role in shaping microbiome composition and dynamics. Is the authors’ analysis consistent with this perspective? Do they expect their conclusions to remain robust if environmental fluctuations are introduced?

We thank the reviewer for stressing this point. The introduction of environmental fluctuations in the model formally violates detailed balance, thereby preventing the definition of an energy function. To date, no study has integrated random interactions together with both demographic and environmental noise within a unified analytical framework. This is certainly a highly promising direction that some of the authors are already exploring. However, given the inherently out-of-equilibrium nature of the system and the absence of a free energy, we would need to adopt a Dynamical Mean-Field Theory formalism and eventually analyze the corresponding stationary equations to be solved self-consistently. We added, however, a brief note in the Discussion section.

(5) The term “order parameters“ may not be intuitive for a biological audience. In any case, the authors should explicitly define each order parameter when first introduced.

We thank the reviewer for the comment. We introduced the names of the order parameters as soon as they are introduced, along with a brief explanation of their meaning that may be accessible to an audience with biological background.

(6) Line 242: Should ψU be ψD?

We thank the reviewer for the observation. We corrected the typo.

(7) Given that the authors are discussing healthy and diseased states and to avoid confusion, the authors could perhaps use another word for ’pathological’ when they refer to dynamical regimes (e.g., in Appendix 2: ’letting the system enter the pathological regime of unbounded growth’).

We thank the reviewer for the helpful comment. As suggested, we used the term “unphysical” instead of “pathological” where needed.

Reviewer #2:

(1) A technical point that I could not understand is how the authors deal with compositional data. One reason for my confusion is that the order parameters h and q0 are fixed n data to 1/S and 1/S2, and thus I do not see how they can be informative. Same for carrying capacity, why is it not 1 if considering relative abundance?

We thank the reviewer for raising this point. We acknowledge that the treatment of compositional data and the interpretation of order parameters h and q0 were not sufficiently clarified in the manuscript. Additionally, there was an imprecision in the text regarding the interpretation of these parameters.

As defined in revised Eq. (4) of the manuscript, h and q0 are to be averaged over the entire dataset, summing across samples α. Specifically, and , where S_α is the number of species present in sample α and is the average over samples. These parameters are therefore informative, as they encapsulate sample-level ecological diversity, and their variation reflects biological differences between healthy and diseased states. For instance, Pasqualini et al., 2024 [4] reported significant differences in these metrics between health conditions, thereby supporting their ecological relevance.

Regarding carrying capacities, we clarify that although we work with relative abundance data (i.e., compositional data), we do not fix the carrying capacity K to 1. Instead, we set K to the maximum value of xi (relative abundance) within each sample, to preserve compatibility with empirical data and allow for coexistence. While this remains a modeling assumption, it ensures better ecological realism within the constraints of the disordered GLV framework.

(2) Obviously I’m missing something, so it would be nice to clarify in simple terms the logic of the argument. I understand that Lagrange multipliers are going to be used in the model analysis, and there are a lot of technical arguments presented in the paper, but I would like a much more intuitive explanation about the way the data can be used to infer order parameters if those are fixed by definition in compositional data.

We thank the reviewer for the observation. The order parameters can be measured directly from the data, even in the presence of compositionality, as explained above. We can connect those parameters with the theory even for compositional data, because the only effect of adding the compositionality constraint is to shift the linear coefficient in the Hamiltonian, which corresponds to shifting the average interaction µ. However, the resulting phase diagram is mostly affected by the variance of the interactions σ2 (as µ is such that we are in the bounded phase).

(3) Another point that I did not understand comes from the fact that the authors claim that interaction variance is smaller in unhealthy microbiomes. Yet they also find that those are closer to instability, and are more driven by niche processes. I would have expected the opposite to be true, more variance in the interactions leading to instability (as in May’s original paper for instance). Is this apparent paradox explained by covariations in demographic stochasticity (T) and immigration rate (lambda)? If so, I think it would be very useful to comment on that.

As Altieri and coworkers showed in their PRL (2021) [5], the phase diagram of our model differs fundamentally from that of Biroli et al. (2018) [6]. In the latter, the intuitive rule – greater interaction variance yields greater instability – indeed holds. For the sake of clarity, we have attached below the resulting phase diagram obtained by Altieri et al.

The apparent paradox arises because the two phase diagrams are tuned by different parameters. Consequently, even at low temperature and with weak interaction variance, our system may sit nearer to the replica-symmetrybreaking (RSB) line.

Fig. 3 in the main text it is not a (σ,T) phase diagram where all other parameters are kept constant. Rather, it is a plot of the inferred σ and T parameters from the data (without showing the corresponding µ).

To capture the full, non-trivial influence of all parameters on stability, we studied the so-called “replicon eigenvalue” in the RS (i.e. single equilibrium) approximation. This leading eigenvalue measures how close a given set of inferred parameters – and hence a microbiome – is to the RSB threshold. For a visual representation of these findings, refer to Figure 4.

Author response image 1.

(4) What do the empirical SAD look like? It would be nice to see the actual data and how the theoretical SADs compare.

The empirical species abundance distributions (SADs) analyzed in our study are presented and discussed in detail in Pasqualini et al., 2024 [4]. Given the overlap in content, we chose not to reproduce these figures in the current manuscript to avoid redundancy.

As we also clarify in the revised text, the theoretical SAD is derived from the disordered generalized Lotka-Volterra (dGLV) model in the unique fixed point phase typically exhibit exponential tails. These distributions do not match the heavier-tailed patterns (e.g., log-normal or power-law-like) observed in empirical microbiome data. This discrepancy stems from the simplifying assumptions of the dGLV framework, including the use of constant carrying capacities and demographic noise.

In the revised manuscript, we have added a brief discussion in the revised manuscript to explicitly acknowledge this limitation and emphasize it as a direction for future refinement of the model, such as incorporating heterogeneous carrying capacities or exploring alternative noise structures.

(5) Some typos: often “niche” is written “nice”.

We thank the reviewer for this suggestion. After inspecting the text, we corrected the reported typos.

Reviewer #3:

Major comments:

(1) In the S3 text, the authors say that filtered metagenomic reads were processed using the software Kaiju. The description of the pipeline does not mention how core genes were selected, which is often a crucial step in determining the abundance of a species in a metagenomic sample. In addition, the senior author of this manuscript has published a version of Kaiju that leverages marker genes classification methods (deemed Core-Kaiju), but it was not used for either this manuscript or Pasqualini et al. (2014; Tovo et al., 2020). I am not suggesting that the data necessarily needs to be reprocessed, but it would be useful to know how core genes were chosen in Pasqualini et al. and why Core-Kaiju was not used (2014).

Prior to the current manuscript and the PLOS Computational Biology paper by Pasqualini et al. [4], we applied the core-Kaiju protocol to the same dataset used in both studies. However, this tool was originally developed and validated using general catalogs of culturable organisms, not specifically tuned for gut microbiomes. As a result, we have realized that in many samples Core Kajiu would filter only very few species (in some samples, the number of identified species was as low as 5–10), undermining the reliability of the analysis. Due to these limitations, we opted to use the standard Kaiju version in our work. We are actively developing an improved version of the core-Kaiju protocol that will overcome the discussed limitations and preliminary results (not shown here) indicate the robustness of the obtained patterns also in this case.

(2) My understanding of Pasqualini et al. was that diseased patients experienced larger fluctuations in abundance, while in this study, they had smaller fluctuations (Figure 3a; 2024). Is this a discrepancy between the two models or is there a more nuanced interpretation?

We thank the reviewer for the observation. This is only an apparent discrepancy, as the term fluctuation has different meanings in the two contexts. The fluctuations referred to by the reviewer correspond to a parameter of our theory—namely, noise in the interactions. Conversely, in Pasqualini et al. σ indicates environmental fluctuations. Nevertheless, there is no conceptual discrepancy in our results: in both studies, unhealthy microbiomes were found to be less stable. In fact, also in this study, notably Fig. 4, shows that unhealthy microbiomes lie closer to the RSB line, a phenomenon that is also associated with enhanced fluctuations.

(3) Line 38-41: It would be helpful to explicitly state what “interaction patterns” are being referenced here. The final sentence could also be clarified. Do microbiomes “host“ interactions or are they better described as a property (“have”, “harbor”). The word “host” may confuse some readers since it is often used to refer to the human host. I am also not sure what point is being made by “expected to govern natural ones”. There are interactions between members of a microbiome; experimental studies have characterized some of these interactions, which we expect to relate in some way to interactions in nature. Is this what the authors are saying?

Thanks. We agree that this sentence was not clear. Indeed, we are referring to pairwise species interactions and not to host-microbiome interactions. We have rewritten this part in the following way: In fact, recent work shows that the network-level properties of species-species interactions —for example, the sign balance, average strength, and connectivity of the inferred interaction matrix— shift systematically between healthy and dysbiotic gut communities (see for instance, [7, 8]). Pairwise species interactions have been quantified in simplified in-vitro consortia [9, 10]; we assume that the same classes of interactions also operate—albeit in a more complex form—in the native gut microbiome.

(4) Line 43: I appreciate that the authors separated neutral vs. logistic models here.

(5) Lines 51-75: The framing here is well-written and convincing. Network inference is an ongoing, active subject in ecology, and there is an unfortunate focus on inferring every individual interaction because ecologists with biology backgrounds are not trained to think about the problem in the language of statistical physics.

We thank the reviewer for these positive comments.

(6) Line 87: Perhaps I’m missing something obvious, but I don’t see how ρi sets the intrinsic timescale of the dynamics when its units are 1/(time*individuals), assuming the dimensions of ri are inverse time.

We thank the reviewer for the observation. We corrected this phrase in the main text.

(7) Lines 189-190: “as close as possible to the data” it would aid the reader if you specified the criteria meant by this statement.

We thank the reviewer for the observation. We removed the sentence, as it introduced some redundancy in our argument. In the subsequent text, the proposed method is exposed in details.

(8) Line 198: It would aid the reader if you provided some context for what the T - σ plane represents.

We thank the referee for the helpful indication. Indeed, we have better clarified the mutual role of the demographic noise amplitude and strength of the random interaction matrix, as theoretically predicted in the PRL (2021) by Altieri and coworkers [5]. Please, find an additional paragraph on page 6 of the resubmitted version.

(9) Line 217: Specifying what is meant by “internal modes“ would aid the typical life science reader.

We thank the reviewer for the suggestion. Recognizing that referring to “internal modes” to describe the SAD shape in that context might cause confusion, we replaced “internal modes“ with “peaks”.

(10) Line 219: Some additional justification and clarification are needed here, as some may think of “m“ as being biomass.

We added a sentence to better explain this concept. “In classical and quantum field theory, the particle-particle interaction embedded in the quadratic term is typically referred to as a mass source. In the context of this study, captures quadratic fluctuations of species abundances, as also appearing in the expression of the leading eigenvalue of the stability matrix.”

Minor comments:

(1) I commend the authors for removing metagenomic reads that mapped to the human genome in the preprocessing stage of their pipeline. This may seem like an obvious pre-processing step, but it is unfortunately not always implemented.

We thank the referee for pointing this potential issue. The data used in this work, as well as the bioinformatic workflow used to generate them has been described in detail in Pasqualini et al., 2024 [4]. As one of the main steps for preprocessing, we remove reads mapping to the human genome.

(2) Line 13: “Bacterial“ excludes archaea, and while you may not have many high-abundance archaea in your human gut data, this sentence does not specify the human gut. Usually, this exclusion is averted via the term “microbial“, though sometimes researchers raise objections to the term when the data does not include fungal members (e.g., all 16S studies).

We thank the reviewer for this suggestion. As to include archaeal organisms, we adopt the term “microbial“ instead of “bacterial“.

(3) Line 18: This manuscript is being submitted under the “Physics of Living Systems“ tract, but it may be useful to explicitly state in the Abstract that disordered systems are a useful approach for understanding large, complex communities for the benefit of life science researchers coming from a biology background.

Thank. We have modified the abstract following this suggestion.

(4) Line 68: Consider using “adapted“ or something similar instead of “mutated“ if there is no specific reason for that word choice.

We thank the reviewer for this suggestion, which was implemented in the text.

(5) Line 111: It would be useful to define annealed and quenched for a general life science audience.

We thank the reviewer for this suggestion. In the “Results” section, we have opted for “time-dependent disordered interactions” to reach a broader audience and avoid any jargon. Moreover, in the Discussion we added a detailed footnote: “In contrast to the quenched approximation, the annealed version assumes that the random couplings are not fixed but instead fluctuate over time, with their covariance governed by independent Ornstein–Uhlenbeck processes.”

(6) Line 124: Likewise for the replicon sector.

We thank the reviewer for the suggestion. We added a footnote on page 4, after the formula, to highlight the physical intuition behind the introduction of the replicon mode.

“The replicon eigenvalue refers to a particular type of fluctuation around the saddle-point (mean-field) solution within the replica framework. When the Hessian matrix of the replicated free energy is diagonalized, fluctuations are divided into three sectors: longitudinal, anomalous, and replicon. The replicon mode is the most sensitive to criticality signaling – by its vanishing trend – the emergence of many nearly-degenerate states. It essentially describes how ‘soft’ the system is to microscopic rearrangements in configuration space.”

(7) Figure 2: It would be helpful to include y-axis labels for each order parameter alongside the mathematical notation.

We thank the reviewer for this suggestion. Now the y-axis of Figure 2 includes, along the mathmetical symbol, the label of the represented quantities.

(8) Line 242: Subscript “U” is used to denote “Unhealthy” microbiomes, but “D” is used to denote “Diseased” in Figs. 2 and 3 (perhaps elsewhere as well).

We thank the reviewer for this observation. After checking the various subscripts in the text, coherently with figure 2 and 3, we homogenized our notation, adopting the subscript “D“ for symbols related to the diseased/unhealthy condition.

(9) Line 283: “not to“ should be “not due to“

We thank the reviewer for this suggestion. After inspecting the text, we corrected the reported error.

(10) Equations 23, 34: Extra “=“ on the RHS of the first line.

We consistently follow the same formatting across all the line breaks in the equations throughout the text.

We are thus resubmitting our paper, hoping to have satisfactorily addressed all referees’ concerns.

References

(1) Jacopo Grilli. Macroecological laws describe variation and diversity in microbial communities. Nature communications, 11(1):4743, 2020.

(2) Guy Bunin. Ecological communities with lotka-volterra dynamics. Physical Review E, 95(4):042414, 2017.

(3) Matthieu Barbier, Jean-Franc¸ois Arnoldi, Guy Bunin, and Michel Loreau. Generic assembly patterns in complex ecological communities. Proceedings of the National Academy of Sciences, 115(9):2156–2161, 2018.

(4) Jacopo Pasqualini, Sonia Facchin, Andrea Rinaldo, Amos Maritan, Edoardo Savarino, and Samir Suweis. Emergent ecological patterns and modelling of gut microbiomes in health and in disease. PLOS Computational Biology, 20(9):e1012482, 2024.

(5) Ada Altieri, Felix Roy, Chiara Cammarota, and Giulio Biroli. Properties of equilibria and glassy phases of the random lotka-volterra model with demographic noise. Physical Review Letters, 126(25):258301, 2021.

(6) Giulio Biroli, Guy Bunin, and Chiara Cammarota. Marginally stable equilibria in critical ecosystems. New Journal of Physics, 20(8):083051, 2018.

(7) Amir Bashan, Travis E Gibson, Jonathan Friedman, Vincent J Carey, Scott T Weiss, Elizabeth L Hohmann, and Yang-Yu Liu. Universality of human microbial dynamics. Nature, 534(7606):259–262, 2016.

(8) Marcello Seppi, Jacopo Pasqualini, Sonia Facchin, Edoardo Vincenzo Savarino, and Samir Suweis. Emergent functional organization of gut microbiomes in health and diseases. Biomolecules, 14(1):5, 2023.

(9) Jared Kehe, Anthony Ortiz, Anthony Kulesa, Jeff Gore, Paul C Blainey, and Jonathan Friedman. Positive interactions are common among culturable bacteria. Science advances, 7(45):eabi7159, 2021.

(10) Ophelia S Venturelli, Alex V Carr, Garth Fisher, Ryan H Hsu, Rebecca Lau, Benjamin P Bowen, Susan Hromada, Trent Northen, and Adam P Arkin. Deciphering microbial interactions in synthetic human gut microbiome communities. Molecular systems biology, 14(6):e8157, 2018.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors develop a novel method to infer ecologically-informative parameters across healthy and diseased states of the gut microbiota, although the method is generalizable to other datasets for species abundances. The authors leverage techniques from theoretical physics of disordered systems to infer different parameters-mean and standard deviation for the strength of bacterial interspecies interactions, a bacterial immigration rate, and the strength of demographic noise-that describe the statistics of microbiota samples from two groups-one for healthy subjects and another one for subjects with chronic inflammation syndromes. To do this, the authors simulate communities with a modified version of the Generalized Lotka-Volterra model and randomly-generated interactions, and then use a moment-matching algorithm to find sets of parameters that better reproduce the data for species abundances. They find that these parameters are different for the healthy and diseased microbiota groups. The results suggest, for example, that bacterial interaction strengths, relative to noise and immigration, are more dominant of microbiota dynamics in diseased states than in healthy states.

We think that this manuscript brings an important contribution that will be of interest in the areas of statistical physics, (microbiota) ecology and (biological) data science. The evidence of their results is solid and the work improves the state-of-the-art in terms of methods.

Strengths:

• Using a fairly generic ecological model, the method can identify the change in the relative importance of different ecological forces (distribution of interspecies interactions, demographic noise and immigration) in different sample groups. The authors focus on the case of the human gut microbiota, showing that the data is consistent with a higher influence of species interactions (relative to demographic noise and immigration) in a disease microbiota state than in healthy ones.

• The method is novel, original and it improves the state-of-the-art methodology for the inference of ecologically-relevant parameters. The analysis provides solid evidence on the conclusions.

Weaknesses:

• As a proof of concept for a new inference method, this text maintains a technical focus, which may require some familiarity with statistical physics. Nevertheless, the authors' clear introduction of key mathematical terms and their interpretations, along with a clear discussion of the ecological implications, make the results accessible and easy to follow.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The study explored the biomechanics of kangaroo hopping across both speed and animal size to try and explain the unique and remarkable energetics of kangaroo locomotion.

Strengths:

The study brings kangaroo locomotion biomechanics into the 21st century. It is a remarkably difficult project to accomplish. There is excellent attention to detail, supported by clear writing and figures.

Weaknesses:

The authors oversell their findings, but the mystery still persists. 

The manuscript lacks a big-picture summary with pointers to how one might resolve the big question.

General Comments

This is a very impressive tour de force by an all-star collaborative team of researchers. The study represents a tremendous leap forward (pun intended) in terms of our understanding of kangaroo locomotion. Some might wonder why such an unusual species is of much interest. But, in my opinion, the classic study by Dawson and Taylor in 1973 of kangaroos launched the modern era of running biomechanics/energetics and applies to varying degrees to all animals that use bouncing gaits (running, trotting, galloping and of course hopping). The puzzling metabolic energetics findings of Dawson & Taylor (little if any increase in metabolic power despite increasing forward speed) remain a giant unsolved problem in comparative locomotor biomechanics and energetics. It is our "dark matter problem".

Thank you for the kind words.

This study is certainly a hop towards solving the problem. But, the title of the paper overpromises and the authors present little attempt to provide an overview of the remaining big issues. 

We have modified the title to reflect this comment.  “Postural adaptations may contribute to the unique locomotor energetics seen in hopping kangaroos”

The study clearly shows that the ankle and to a lesser extent the mtp joint are where the action is. They clearly show in great detail by how much and by what means the ankle joint tendons experience increased stress at faster forward speeds.

Since these were zoo animals, direct measures were not feasible, but the conclusion that the tendons are storing and returning more elastic energy per hop at faster speeds is solid. The conclusion that net muscle work per hop changes little from slow to fast forward speeds is also solid. 

Doing less muscle work can only be good if one is trying to minimize metabolic energy consumption. However, to achieve greater tendon stresses, there must be greater muscle forces. Unless one is willing to reject the premise of the cost of generating force hypothesis, that is an important issue to confront. Further, the present data support the Kram & Dawson finding of decreased contact times at faster forward speeds. Kram & Taylor and subsequent applications of (and challenges to) their approach supports the idea that shorter contact times (tc) require recruiting more expensive muscle fibers and hence greater metabolic costs. Therefore, I think that it is incumbent on the present authors to clarify that this study has still not tied up the metabolic energetics across speed problems and placed a bow atop the package. 

Fortunately, I am confident that the impressive collective brain power that comprises this author list can craft a paragraph or two that summarizes these ideas and points out how the group is now uniquely and enviably poised to explore the problem more using a dynamic SIMM model that incorporates muscle energetics (perhaps ala' Umberger et al.). Or perhaps they have other ideas about how they can really solve the problem.

You have raised important points, thank you for this feedback. We have added a limitations and considerations section to the discussion which highlights that there are still unanswered questions. Line 311-328

Considerations and limitations

“First, we believe it is more likely that the changes in moment arms and EMA can be attributed to speed rather than body mass, given the marked changes in joint angles and ankle height observed at faster hopping speeds. However, our sample included a relatively narrow range of body masses (13.7 to 26.6 kg) compared to the potential range (up to 80 kg), limiting our ability to entirely isolate the effects of speed from those of mass. Future work should examine a broader range of body sizes. Second, kangaroos studied here only hopped at relatively slow speeds, which bounds our estimates of EMA and tendon stress to a less critical region. As such, we were unable to assess tendon stress at fast speeds, where increased forces would reduce tendon safety factors closer to failure. A different experimental or modelling approach may be needed, as kangaroos in enclosures seem unwilling to hop faster over force plates. Finally, we did not determine whether the EMA of proximal hindlimb joints (which are more difficult to track via surface motion capture markers) remained constant with speed. Although the hip and knee contribute substantially less work than the ankle joint (Fig. 4), the majority of kangaroo skeletal muscle is located around these proximal joints. A change in EMA at the hip or knee could influence a larger muscle mass than at the ankle, potentially counteracting or enhancing energy savings in the ankle extensor muscle-tendon units. Further research is needed to understand how posture and muscles throughout the whole body contribute to kangaroo energetics.”

Additionally, we added a line “Peak GRF also naturally increased with speed together with shorter ground contact durations (Fig. 2b, Suppl. Fig 1b)” (line 238) to highlight that we are not proposing that changes in EMA alone explain the full increase in tendon stress. Both GRF and EMA contribute substantially (almost equally) to stress, and we now give more equal discussion to both. For instance, we now also evaluate how much each contributes: “If peak GRF were constant but EMA changed from the average value of a slow hop to a fast hop, then stress would increase 18%, whereas if EMA remained constant and GRF varied by the same principles, then stress would only increase by 12%. Thus, changing posture and decreasing ground contact duration both appear to influence tendon stress for kangaroos, at least for the range of speeds we examined” (Line 245-249)

We have added a paragraph in the discussion acknowledging that the cost of generating force problem is not resolved by our work, concluding that “This mechanism may help explain why hopping macropods do not follow the energetic trends observed in other species (Dawson and Taylor 1973, Baudinette et al. 1992, Kram and Dawson 1998), but it does not fully resolve the cost of generating force conundrum” Line 274-276.

I have a few issues with the other half of this study (i.e. animal size effects). I would enjoy reading a new paragraph by these authors in the Discussion that considers the evolutionary origins and implications of such small safety factors. Surely, it would need to be speculative, but that's OK.

We appreciate this comment from the reviewer, however could not extend the study to discuss animal size effects because, as we now note in the results: “The range of body masses may not be sufficient to detect an effect of mass on ankle moment in addition to the effect of speed.” Line 193

Reviewer #2 (Public Review):

Summary

This is a fascinating topic that has intrigued scientists for decades. I applaud the authors for trying to tackle this enigma. In this manuscript, the authors primarily measured hopping biomechanics data from kangaroos and performed inverse dynamics. 

While these biomechanical analyses were thorough and impressively incorporated collected anatomical data and an Opensim model, I'm afraid that they did not satisfactorily address how kangaroos can hop faster and not consume more metabolic energy, unique from other animals.  Noticeably, the authors did not collect metabolic data nor did they model metabolic rates using their modelling framework. Instead, they performed a somewhat traditional inverse dynamics analysis from multiple animals hopping at a self-selected speed.

In the current study, we aimed to provide a joint-level explanation for the increases of tendon stress that are likely linked to metabolic energy consumption.

We have now included a limitations section in the manuscript (See response to Rev 1). We plan to expand upon muscle level energetics in the future with a more detailed musculoskeletal model.

Within these analyses, the authors largely focused on ankle EMA, discussing its potential importance (because it affects tendon stress, which affects tendon strain energy, which affects muscle mechanics) on the metabolic cost of hopping. However, EMA was roughly estimated (CoP was fixed to the foot, not measured) and did not detectibly associate with hopping speed (see results Yet, the authors interpret their EMA findings as though it systematically related with speed to explain their theory on how metabolic cost is unique in kangaroos vs. other animals

As noted in our methods, EMA was not calculated from a fixed centre of pressure (CoP). We did fix the medial-lateral position, owing to the fact that both feet contacted the force plate together, but the anteroposterior movement of the CoP was recorded by the force plate and thus allowed to move. We report the movement (or lack of movement) in our results. The anterior-posterior axis is the most relevant to lengthening or shortening the distance of the ‘out-lever’ R, and thereby EMA. It is necessary to assume fixed medial-lateral position because a single force trace and CoP is recorded when two feet land on the force plate. The mediallateral forces on each foot cancel out so there is no overall medial-lateral movement if the forces are symmetrical (e.g. if the kangaroo is hopping in a straight path and one foot is not in front of the other). We only used symmetrical trials so that the anterior-posterior movement of the CoP would be reliable. We have now added additional details into the text to clarify this

Indeed, the relationship between R and speed (and therefore EMA and speed) was not significant. However, the significant change in ankle height with speed, combined with no systematic change in COP at midstance, demonstrates that R would be greater at faster speeds. If we consider the nonsignificant relationship between R and speed to indicate that there is no change in R, then these two results conflict. We could not find a flaw in our methods, so instead concluded that the nonsignificant relationship between R and speed may be due to a small change in R being undetectable in our data. Taking both results into account, we believe it is more likely that there is a non-detectable change in R, rather than no change in R with speed, but we presented both results for transparency. We have added an additional section into the results to make this clearer (Line 177-185) “If we consider the nonsignificant relationship between R (and EMA) and speed to indicate that there is no change in R, then it conflicts with the ankle height and CoP result. Taking both into account, we think it is more likely that there is a small, but important, change in R, rather than no change in R with speed. It may be undetectable because we expect small effect sizes compared to the measurement range and measurement error (Suppl. Fig. 3h), or be obscured by a similar change in R with body mass. R is highly dependent on the length of the metatarsal segment, which is longer in larger kangaroos (1 kg BM corresponded to ~1% longer segment, P<0.001, R²=0.449). If R does indeed increase with speed, both R and r will tend to decrease EMA at faster speeds.”

These speed vs. biomechanics relationships were limited by comparisons across different animals hopping at different speeds and could have been strengthened using repeated measures design

There is significant variation in speed within individuals, not just between individuals. The preferred speed of kangaroos is 2-4.5 m/s, but most individuals showed a wide speed range within this. Eight of our 16 kangaroos had a maximum speed that was 1-2m/s faster than their slowest trial. Repeated measures of these eight individuals comprises 78 out of the 100 trials.   It would be ideal to collect data across the full range of speeds for all individuals, but it is not feasible in this type of experimental setting. Interference with animals such as chasing is dangerous to kangaroos as they are prone to adverse reactions to stress. We have now added additional information about the chosen hopping speeds into the results and methods sections to clarify this “The kangaroos elected to hop between 1.99 and 4.48 m s^-1, with a range of speeds and number of trials for each individual (Suppl. Fig. 9).”  (Line 381-382)

There are also multiple inconsistencies between the authors' theory on how mechanics affect energetics and the cited literature, which leaves me somewhat confused and wanting more clarification and information on how mechanics and energetics relate

We thank the reviewer for this comment. Upon rereading we now understand the reviewers position, and have made substantial revisions to the introduction and discussion (See comments below) 

My apologies for the less-than-favorable review, I think that this is a neat biomechanics study - but am unsure if it adds much to the literature on the topic of kangaroo hopping energetics in its current form.

Again we thank the reviewer for their time and appreciate their efforts to strengthen our manuscript.

Reviewer #3 (Public Review):

Summary:

The goal of this study is to understand how, unlike other mammals, kangaroos are able to increase hopping speed without a concomitant increase in metabolic cost. They use a biomechanical analysis of kangaroo hopping data across a range of speeds to investigate how posture, effective mechanical advantage, and tendon stress vary with speed and mass. The main finding is that a change in posture leads to increasing effective mechanical advantage with speed, which ultimately increases tendon elastic energy storage and returns via greater tendon strain. Thus kangaroos may be able to conserve energy with increasing speed by flexing more, which increases tendon strain.

Strengths:

The approach and effort invested into collecting this valuable dataset of kangaroo locomotion is impressive. The dataset alone is a valuable contribution.

Thank you!

Weaknesses:

Despite these strengths, I have concerns regarding the strength of the results and the overall clarity of the paper and methods used (which likely influences how convincingly the main results come across).

(1) The paper seems to hinge on the finding that EMA decreases with increasing speed and that this contributes significantly to greater tendon strain estimated with increasing speed. It is very difficult to be convinced by this result for a number of reasons:

It appears that kangaroos hopped at their preferred speed. Thus the variability observed is across individuals not within. Is this large enough of a range (either within or across subjects) to make conclusions about the effect of speed, without results being susceptible to differences between subjects? 

Apologies, this was not clear in the manuscript. Kangaroos hopping at their preferred speed means we did not chase or startle them into high speeds to comply with ethics and enclosure limitations. Thus we did not record a wide range of speeds within the bounds of what kangaroos are capable of in the wild (up to 12 m/s), but for the range we did measure (~2-4.5 m/s), there is a large amount of variation in hopping speed within each individual kangaroo. Out of 16 individuals, eight individuals had a difference of 1-2m/s between their slowest and fastest trials, and these kangaroos accounted for 78 out of 100 trials. Of the remainder, six individuals had three for fewer trials each, and two individuals had highly repeatable speeds (3 out of 4, and 6 out of 7 trials were within 0.5 m/s). We have now removed the terminology “preferred speed” e.g line 115. We have added additional information about the chosen hopping speeds into the results and methods, including an appendix figure “The kangaroos elected to hop between 1.99 and 4.48 m s^-1, with a range of speeds and number of trials for each individual (Suppl. Fig. 9).” (Line 381-382)

In the literature cited, what was the range of speeds measured, and was it within or between subjects?

For other literature, to our knowledge the highest speed measured is ~9.5m/s (see supplementary Fig1b) and there were multiple measures for several individuals (see methods Kram & Dawson 1998). 

Assuming that there is a compelling relationship between EMA and velocity, how reasonable is it to extrapolate to the conclusion that this increases tendon strain and ultimately saves metabolic cost?  They correlate EMA with tendon strain, but this would still not suggest a causal relationship (incidentally the p-value for the correlation is not reported). 

The functions that underpin these results (e.g. moment = GRF*R) come from physical mechanics and geometry, rather than statistical correlations. Additionally, a p-value is not appropriate in the relationship between EMA and stress (rather than strain) because the relationship does not appear to be linear. We have made it clearer in the discussion that we are not proposing that entire change in stress is caused by changes in EMA, but that the increase in GRF that naturally occurs with speed will also explain some of the increase in stress, along with other potential mechanisms. The discussion has been extensively revised to reflect this. 

Tendon strain could be increasing with ground reaction force, independent of EMA. Even if there is a correlation between strain and EMA, is it not a mathematical necessity in their model that all else being equal, tendon stress will increase as ema decreases? I may be missing something, but nonetheless, it would be helpful for the authors to clarify the strength of the evidence supporting their conclusions.

Yes, GRF also contributes to the increase in tendon stress in the mechanism we propose (Suppl. Fig. 8), see the formulas in Fig 6, and we have made this clearer in the revised discussion (see above comment).  You are correct that mathematically stress is inversely proportional to EMA, which can be observed in Fig. 7a, and we did find that EMA decreases. 

The statistical approach is not well-described. It is not clear what the form of the statistical model used was and whether the analysis treated each trial individually or grouped trials by the kangaroo. There is also no mention of how many trials per kangaroo, or the range of speeds (or masses) tested. 

The methods include the statistical model with the variables that we used, as well as the kangaroo masses (13.7 to 26.6 kg, mean: 20.9 ± 3.4 kg). We did not have sufficient within individual sample size to use a linear mixed effect model including subject as a random factor, thus all trials were treated individually. We have included this information in the results section. 

We have now moved the range of speeds from the supplementary material to the results and figure captions. We have added information on the number of trials per kangaroo to the methods, and added Suppl. Fig. 9 showing the distribution of speeds per kangaroo.

We did not group the data e.g. by using an average speed per individual for all their trials, or by comparing fast to slow groups for statistical analysis (the latter was only for display purposes in our figures, which we have now made clearer in the methods statistics section). 

Related to this, there is no mention of how different speeds were obtained. It seems that kangaroos hopped at a self-selected pace, thus it appears that not much variation was observed. I appreciate the difficulty of conducting these experiments in a controlled manner, but this doesn’t exempt the authors from providing the details of their approach.

Apologies, this was not clear in the manuscript. Kangaroos hopping at their preferred speed means we did not chase or startle them into high speeds to comply with ethics and enclosure limitations. Thus we did not record a wide range of speeds within the bounds of what kangaroos are capable of in the wild (up to 12 m/s). We have now removed the terminology “preferred speed” e.g. line 115. We have added additional information about the chosen hopping speeds into the results and methods, including an appendix figure (see above comment). (Line 381-382)

Some figures (Figure 2 for example) present means for one of three speeds, yet the speeds are not reported (except in the legend) nor how these bins were determined, nor how many trials or kangaroos fit in each bin. A similar comment applies to the mass categories. It would be more convincing if the authors plotted the main metrics vs. speed to illustrate the significant trends they are reporting.

Thank you for this comment. The bins are used only for display purposes and not within the statistical analysis. We have clarified this in the revised manuscript: “The data was grouped into body mass (small 17.6±2.96 kg, medium 21.5±0.74 kg, large 24.0±1.46 kg) and speed (slow 2.52±0.25 m s^-1, medium 3.11±0.16 m s^-1, fast 3.79±0.27 m s^-1) subsets for display purposes only”. (Line 495-497)

(2) The significance of the effects of mass is not clear. The introduction and abstract suggest that the paper is focused on the effect of speed, yet the effects of mass are reported throughout as well, without a clear understanding of the significance. This weakness is further exaggerated by the fact that the details of the subject masses are not reported.

Indeed, the primary aim of our study was to explore the influence of speed, given the uncoupling of energy from hopping speed in kangaroos. We included mass to ensure that the effects of speed were not driven by body mass (i.e.: that larger kangaroos hopped faster). Subject masses were reported in the first paragraph of the methods, albeit some were estimated as outlined in the same paragraph.

(3) The paper needs to be significantly re-written to better incorporate the methods into the results section. Since the results come before the methods, some of the methods must necessarily be described such that the study can be understood at some level without turning to the dedicated methods section. As written, it is very difficult to understand the basis of the approach, analysis, and metrics without turning to the methods.

The methods after the discussion is a requirement of the journal. We have incorporated some methods in the results where necessary but not too repetitive or disruptive, e.g. Fig. 1 caption, and specifying we are only analysing EMA for the ankle joint

Reviewing Editor (Recommendations For The Authors):

Below is a list of specific recommendations that the authors could address to improve the eLife assessment:

(1) Based on the data presented and the fact that metabolic energy was not measured, the authors should temper their conclusions and statements throughout the manuscript regarding the link between speed and metabolic energy savings. We recommend adding text to the discussion summarizing the strengths and limitations of the evidence provided and suggesting future steps to more conclusively answer this mystery.

There is a significant body of work linking metabolic energy savings to measured increases in tendon stress in macropods. However, the purpose of this paper was to address the unanswered questions about why tendon stress increases. We found that stress did not only increase due to GRF increasing with speed as expected, but also due to novel postural changes which decreased EMA. In the revised manuscript, we have tempered our conclusions to make it clearer that it is not just EMA affecting stress, and added limitations throughout the manuscript (see response to Rev 1). 

(2) To provide stronger evidence of a link between speed, mechanics, and metabolic savings the authors can consider estimating metabolic energy expenditure from their OpenSIM model. This is one suggestion, but the authors likely have other, possibly better ideas. Such a model should also be able to explain why the metabolic rate increases with speed during uphill hopping.

Extending the model to provide direct metabolic cost estimates will be the goal of a future paper, however the models does not have detailed muscle characteristics to do this in the formulation presented here. It would be a very large undertaking which is beyond the scope of the current manuscript. As per the comment above, the results of this paper are not reliant on metabolic performance. 

(3) The authors attempt to relate the newly quantified hopping biomechanics to previously published metabolic data. However, all reviewers agree that the logic in many instances is not clear or contradictory. Could one potential explanation be that at slow speeds, forces and tendon strain are small, and thus muscle fascicle work is high? Then, with faster speeds, even though the cost of generating isometric force increases, this is offset by the reduction in the metabolic cost of muscular work. The paper could provide stronger support for their hypotheses with a much clearer explanation of how the kinematics relate to the mechanics and ultimately energy savings.

In response to the reviewers comments, we have substantially modified the discussion to provide clearer rationale.

(4) The methods and the effort expended to collect these data are impressive, but there are a number of underlying assumptions made that undermine the conclusions. This is due partly to the methods used, but also the paper's incomplete description of their methods. We provide a few examples below:

It would be helpful if the authors could speak to the effect of the limited speeds tested and between-animal comparisons on the ability to draw strong conclusions from the present dataset. ·

Throughout the discussion, the authors highlight the relationship between EMA and speed. However, this is misleading since there was no significant effect of speed on EMA. Speed only affected the muscle moment arm, r. At minimum, this should be clarified and the effect on EMA not be overstated. Additionally, the resulting implications on their ability to confidently say something about the effect of speed on muscle stress should be discussed. 

We have now provided additional details, (see responses above) to these concerns. For instance, we added a supplementary figure showing the speed distribution per individual. The primary reviewer concern (that each kangaroo travelled at a single speed) was due to a miscommunication around the terminology “preferred” which has now been corrected. 

We now elaborate in the results why we are not very concerned that EMA is insignificant. The statistical insignificance of EMA is ultimately due to the insignificance of the direct measurement of R, however, we now better explain in the results why we believe that this statistical insignificance is due to error/noise of the measurement which is relatively large compared to the effect size. Indirect indications of how R may increase with speed (via ankle height from the ground) are statistically significant. Lines 177-185. 

We consider this worth reporting because, for instance, an 18% change in EMA will be undetectable by measurement, but corresponds to an 18% change in tendon stress which is measurable and physiologically significant (safety factor would decrease from 2 to 1.67).  We presented both significant and insignificant results for transparency. 

We have also discussed this within a revised limitations section of the manuscript (Line 311328). 

Reviewer #1 (Recommendations For The Authors):

Title: I would cut the first half of the title. At least hedge it a bit. "Clues" instead of "Unlocking the secrets".

We have revised the title to: “Postural adaptations may contribute to the unique locomotor energetics seen in hopping kangaroos”

In my comments, ... typically indicates a stylistic change suggested to the text.

Overall, the paper covers speed and size. Unfortunately, the authors were not 100% consistent in the order of presenting size then speed, or speed then size. Just choose one and stick with it.

We have attempted to keep the order of presenting size and speed consistent, however there are several cases where this would reduce the readability of the manuscript and so in some cases this may vary. 

One must admit that there is a lot of vertical scatter in almost all of the plots. I understand that these animals were not in a lab on a treadmill at a controlled speed and the animals wear fur coats so marker placements vary/move etc. But the spread is quite striking, e.g. Figure 5a the span at one speed is almost 10x. Can the authors address this somewhere? Limitations section?

The variation seen likely results from attempting to display data in a 2D format, when it is in fact the result of multiple variables, including speed, mass, stride frequency and subject specific lengths. Slight variations in these would be expected to produce some noise around the mean, and I think it’s important to consider this while showing the more dominant effects. 

In many locations in the manuscript, the term "work" is used, but rarely if ever specified that this is the work "per hop". The big question revolves around the rate of metabolic energy consumption (i.e. energy per time or average metabolic power), one must not forget that hop frequency changes somewhat across speed, so work per hop is not the final calculation.

Thank you for this comment. We have now explicitly stated work per hop in figure captions and in the results (line 208). The change in stride frequency at this range of speeds is very small, particularly compared to the variance in stride frequency (Suppl. Fig. 1d), which is consistent with other researchers who found that stride frequency was constant or near constant in macropods at analogous speeds (e.g. Dawson and Taylor 1973, Baudinette et al. 1987). 

Line 61 ....is likely related.

Added “likely” (line 59)

Line 86 I think the Allen reference is incomplete. Wasn't it in J Exp Biology?

Thank you. Changed. 

Line 122 ... at faster speeds and in larger individuals.

Changed: “We hypothesised that (i) the hindlimb would be more crouched at faster speeds, primarily due to the distal hindlimb joints (ankle and metatarsophalangeal), independent of changes with body mass” (Line 121-122).

Line 124 I found this confusing. Try to re-word so that you explain you mean more work done by the tendons and less by the ankle musculature.

Amended: “changes in moment arms resulting from the change in posture would contribute to the increase in tendon stress with speed, and may thereby contribute to energetic savings by increasing the amount of positive and negative work done by the ankle without requiring additional muscle work” (Line 123)

Line 129 hopefully "braking" not "breaking"!

Thank you. Fixed. (Line 130)

Line 129 specify fore-aft horizontal force.

Added "fore-aft" to "negative fore-aft horizontal component" (Line 130-131)

Line 130 add something like "of course" or "naturally" since if there is zero fore-aft force, the GRF vector of course must be vertical. 

Added "naturally" (Line 132)

Line 138 clarify that this section is all stance phase. I don't recall reading any swing phase data.

Changed to: "Kangaroo hindlimb stance phase kinematics varied…" (Line 141)

Line 143 and elsewhere. I found the use of dorsiflexion and plantarflexion confusing. In Figure 3, I see the ankle never flexing more than 90 degrees. So, the ankle joint is always in something of a flexed position, though of course it flexes and extends during contact. I urge the authors to simplify to flextion/extension and drop the plantar/dorsi.

We have edited this section to describe both movements as greater extension (plantarflexion). (Line 147). We have further clarified this in the figure caption for figure 3.  

Line 147 ...changes were…

Fixed, line 150

Line 155 I'm a bit confused here. Are the authors calculating some sort of overall EMA or are they saying all of the individual joint EMAs all decreased?

Thank you, we clarified that it is at the ankle. Line 158

Line 158 since kangaroos hop and are thus positioned high and low throughout the stance phase, try to avoid using "high" and "low" for describing variables, e.g. GRF or other variables. Just use "greater/greatest" etc.

Thanks for this suggestion. We have changed "higher" into "greater" where appropriate throughout the manuscript e.g. line 161

Lines 162 and 168 same comment here about "r" and "R". Do you mean ankle or all joints?

Clarified that it is the gastrocnemius and plantaris r, and the R to the ankle. (Lines 164-165)

Line 173 really, ankle height?

Added: ankle height is "vertical distance from the ground". Line 177

Line 177 is this just the ankle r?

Added "of the ankle" line 158 and “Achilles” line 187 

Line 183 same idea, which tendon/tendons are you talking about here?

Added "Achilles" to be more clear (Line 187)

Line 195 substitute "converted" for "transferred".

Done (Line 210)

Line 223 why so vague? i.e. why use "may"? Believe in your data. ...stress was also modulated by changes....

Changed "may" to "is"

Line 229 smaller ankle EMA (especially since you earlier talked about ankle "height").

Changed “lower” to “smaller” Line 254

Line 2236 ...and return elastic energy…

Added "elastic" line 262

Line 244 IMPORTANT: Need to explain this better! I think you are saying that the net work at the ankle is staying the same across speed, BUT it is the tendons that are storing and returning that work, it's not that the muscles are doing a lot of negative/positive work.

Changed: “The consistent net work observed among all speeds suggests the ankle extensor muscle-tendon units are performing similar amounts of ankle work independent of speed, which would predominantly be done by the tendon.” Line 270-272)

Line 258-261 I think here is where you are over-selling the data/story. Although you do say "a" mechanism (and not "the" mechanism, you still need to deal with the cost of generating more force and generating that force faster.

We removed this sentence and replaced it with a discussion of the cost of generating force hypothesis, and alternative scenarios for the how force and metabolics could be uncoupled. 

Line 278 "the" tendon? Which tendon?

Added "Achilles"

Line 289. I don't think one can project into the past.

Changed “projected” to "estimated"

Line 303 no problem, but I've never seen a paper in biology where the authors admit they don't know what species they were studying!

Can’t be helped unfortunately. It is an old dataset and there aren’t photos of every kangaroo. Fortunately, from the grey and red kangaroos we can distinguish between, we know there are no discernible species effects on the data. 

Lines 304-306 I'm not clear here. Did you use vertical impulse (and aerial time) to calculate body weight? Or did you somehow use the braking/propulsive impulse to calculate mass? I would have just put some apples on the force plate and waited for them to stop for a snack.

Stationary weights were recorded for some kangaroos which did stand on the force plate long enough, but unfortunately not all of them were willing to do so. In those cases, yes, we used impulse from steady-speed trials to estimate mass. We cross-checked by estimated mass from segment lengths (as size and mass are correlated). This is outlined in the first paragraph of the methods.

Lines 367 & 401 When you use the word "scaled" do you mean you assumed geometric similarity?

No, rather than geometric scaling, we allowed scaling to individual dimensions by using the markers at midstance for measurements. We have amended the paragraph to clarify that the shape of the kangaroo changes and that mass distribution was preserved during the shape change (line 441-446) 

Lines 381-82 specify "joint work"

Added "joint work"  (Line 457)

Figure 1 is gorgeous. Why not add the CF equation to the left panel of the caption?

We decided to keep the information in the figure caption. “Total leg length was calculated as the sum of the segment lengths (solid black lines) in the hindlimb and compared to the pelvisto-toe distance (dashed line) to calculate the crouch factor”

Figure 2 specify Horizontal fore-aft.

Done

Figure 3g I'd prefer the same Min. Max Flexion vertical axis labels as you use for hip & knee.

While we appreciate the reviewer trying to increase the clarity of this figure, we have left it as plantar/dorsi flexion since these are recognised biomechanical terms. To avoid confusion, we have further defined these in the figure caption “For (f-g), increased plantarflexion represents a decrease in joint flexion, while increased dorsiflexion represents increased flexion of the joint.”

Figure 4. I like it and I think that you scaled all panels the same, i.e. 400 W is represented by the same vertical distance in all panels. But if that's true, please state so in the Caption. It's remarkable how little work occurs at the hip and knee despite the relatively huge muscles there.

Is it true that the y axes are all at the same scale. We have added this to the caption. 

Figure 5 Caption should specify "work per hop".

Added

Figure 7 is another beauty.

Thank you!

Supplementary Figure 3 is this all ANKLE? Please specify.

Clarified that it is the gastrocnemius and plantaris r, and the R to the ankle.

Reviewer #2 (Recommendations For The Authors):

To 'unlock the secrets of kangaroo locomotor energetics' I expected the authors to measure the secretive outcome variable, metabolic rate using laboratory measures. Rather, the authors relied on reviewing historic metabolic data and collecting biomechanics data across different animals, which limits the conclusions of this manuscript.

We have revised to the title to make it clearer that we are investigating a subset of the energetics problem, specifically posture. “Postural adaptations may contribute to the unique locomotor energetics seen in hopping kangaroos.” We have also substantially modified the discussion to temper the conclusions from the paper. 

After reading the hypothesis, why do the authors hypothesize about joint flexion and not EMA? Because the following hypothesis discusses the implications of moment arms on tendon stress, EMA predictions are more relevant (and much more discussed throughout the manuscript).

Ankle and MTP angles are the primary drivers of changes in r, R & thus, EMA. We used a two part hypothesis to capture this. We have rephased the hypotheses: “We hypothesised that (i) the hindlimb would be more crouched at faster speeds, primarily due to the distal hindlimb joints (ankle and metatarsophalangeal), independent of changes with body mass, and (ii) changes in moment arms resulting from the change in posture would contribute to the increase in tendon stress with speed, and may thereby contribute to energetic savings by increasing the amount of positive and negative work done by the ankle without requiring additional muscle work.”

If there were no detectable effects of speed on EMA, are kangaroos mechanically like other animals (Biewener Science 89 & JAP 04) who don't vary EMA across speeds? Despite no detectible effects, the authors state [lines 228-229] "we found larger and faster kangaroos were more crouched, leading to lower ankle EMA". Can the authors explain this inconsistency? Lines 236 "Kangaroos appear to use changes in posture and EMA". I interpret the paper as EMA does not change across speed.

Apologies, we did not sufficiently explain this originally. We now explain in the results our reasoning behind our belief that EMA and R may change with speed. “If we consider the nonsignificant relationship between R (and EMA) and speed to indicate that there is no change in R, then it conflicts with the ankle height and CoP result. Taking both into account, we think it is more likely that there is a small, but important, change in R, rather than no change in R with speed. It may be undetectable because we expect small effect sizes compared to the measurement range and measurement error (Suppl. Fig. 3h), or be obscured by a similar change in R with body mass. R is highly dependent on the length of the metatarsal segment, which is longer in larger kangaroos (1 kg BM corresponded to ~1% longer segment, P<0.001, R²=0.449). If R does indeed increase with speed, both R and r will tend to decrease EMA at faster speeds.” (Line 177-185)

Lines 335-339: "We assumed the force was applied along phalanx IV and that there was no medial or lateral movement of the centre of pressure (CoP)". I'm confused, did the authors not measure CoP location with respect to the kangaroo limb? If not, this simple estimation undermines primary results (EMA analyses).

We have changed "The anterior or posterior movement of the CoP was recorded by the force plate" to read: "The fore-aft movement of the CoP was recorded by the force plate within the motion capture coordinate system" (Line 406-407) and added more justification for fixing the CoP movement in the other axis: “It was necessary to assume the CoP was fixed in the mediallateral axis because when two feet land on the force plate, the lateral forces on each foot are not recorded, and indeed cancel if the forces are symmetrical (i.e. if the kangaroo is hopping in a straight path and one foot is not in front of the other). We only used symmetrical trials to ensure reliable measures of the anterior-posterior movement of the CoP.” (Line 408-413)

The introduction makes many assertions about the generalities of locomotion and the relationship between mechanics and energetics. I'm afraid that the authors are selectively choosing references without thoroughly evaluating alternative theories. For example, Taylor, Kram, & others have multiple papers suggesting that decreasing EMA and increasing muscle force (and active muscle volume) increase metabolic costs during terrestrial locomotion. Rather, the authors suggest that decreasing EMA and increasingly high muscle force at faster speeds don't affect energetics unless muscle work increases substantially (paragraph 2)? If I am following correctly, does this theory conflict with active muscle volume ideas that are peppered throughout this manuscript?

Yes, as you point out, the same mechanism does lead to different results in kangaroos vs humans, for instance, but this is not a contradiction. In all species, decreasing EMA will result in an increase in muscle force due to less efficient leverage (i.e. lower EMA) of the muscles, and the muscle-tendon unit will be required to produce more force to balance the joint moment. As a consequence, human muscles activate a greater volume in order for the muscle-tendon unit to increase muscle work and produce enough force. We are proposing that in kangaroos, the increase in work is done by the achilles tendon rather than the muscles. Previous research suggests that macropod ankle muscles contract isometrically or that the fibres do not shorten more at faster speeds i.e. muscle work does not increase with speed. Instead, the additional force seems to come from the tendon storing and subsequently returning more strain energy (indicated by higher stress). We found that the increase in tendon stress comes from higher ground force at faster speeds, and from it adopting a more crouched posture which increases the tendons’ stresses compared to an upright posture for a given speed (think of this as increasing the tendon’s stress capacity). We have substantially revised the discussion to highlight this.

Similarly, does increased gross or net tendon mechanical energy storage & return improve hopping energetics? Would more tendon stress and strain energy storage with a given hysteresis value also dissipate more mechanical energy, requiring leg muscles to produce more net work? Does net or gross muscle work drive metabolic energy consumption?

Based on the cost of generating force hypothesis, we think that gross muscle work would be linked to driving metabolic energy consumption. Our idea here is that the total body work is a product of the work done by the tendon and the muscle combined. If the tendon has the potential to do more work, then the total work can increase without muscle work needing to increase.

The results interpret speed effects on biomechanics, but each kangaroo was only collected at 1 speed. Are inter-animal comparisons enough to satisfy this investigation?

We have added a figure (Suppl Fig 9) to demonstrate the distribution of speed and number of trials per kangaroo. We have also removed "preferred" from the manuscript as this seems to cause confusion. Most kangaroos travelled at a range of “casual” speeds.

Abstract: Can the authors more fully connect the concept of tendon stress and low metabolic rates during hopping across speeds? Surely, tendon mechanics don't directly drive the metabolic cost of hopping, but they affect muscle mechanics to affect energetics.

Amended to: " This phenomenon may be related to greater elastic energy savings due to increasing tendon stress; however, the mechanisms which enable the rise in stress, without additional muscle work remain poorly understood." (Lines 25-27).

The topic sentence in lines 61-63 may be misleading. The ensuing paragraph does not substantiate the topic sentence stating that ankle MTUs decouple speeds and energetics.

We added "likely" to soften the statement. (Line 59)

Lines 84-86: In humans, does more limb flexion and worse EMA necessitate greater active muscle volume? What about muscle contractile dynamics - See recent papers by Sawicki & colleagues that include Hill-type muscle mechanics in active muscle volume estimates.

Added: “Smaller EMA requires greater muscle force to produce a given force on the ground, thereby demanding a greater volume of active muscle, and presumably greater metabolic rates than larger EMA for the same physiology”. (Line 80-82)

Lines 106: can you give the context of what normal tendon safety factors are?

Good idea. Added: "far lower than the typical safety factor of four to eight for mammalian tendons (Ker et al. 1988)." Line 106-107

I thought EMA was relatively stable across speeds as per Biewener [Science & JAP '04]. However the authors gave an example of an elephant to suggest that it is typically inversely related to speed. Can the authors please explain the disconnect and the most appropriate explanation in this paragraph?

Knee EMA in particular changed with speed in Biewener 2004. What is “typical” probably depends on the group of animals studied; e.g., cursorial quadrupedal mammals generally seem to maintain constant EMA, but other groups do not.

These cases are presented to show a range of consequences for changing EMA (usually with mass, but sometimes with speed). We have made several adjustments to the paragraph to make this clearer. Lines 85-93.

The results depend on the modeled internal moment arm (r). How confident are the authors in their little r prediction? Considering complications of joint mechanics in vivo including muscle bulging. Holzer et al. '20 Sci Rep demonstrated that different models of the human Achilles tendon moment arm predict vastly different relationships between the moment arm and joint angle.

Our values for r and EMA closely align with previous papers which measured/calculate these values in kangaroos, such as Kram 1998, and thus we are confident in our interpretation.  

This is a misleading results sentence: Small decreases in EMA correspond to a nontrivial increase in tendon stress, for instance, reducing EMA from 0.242 (mean minimum EMA of the slow group) to 0.206 (mean minimum EMA of the fast group) was associated with an ~18% increase in tendon stress. The authors could alternatively say that a ~15% decrease in EMA was associated with an ~18% increase in tendon stress, which seems pretty comparable.

Thank you for pointing this out, it is important that it is made clearer. Although the change in relative magnitude is approximately the same (as it should be), this does not detract from the importance. The "small decrease in EMA" is referring to the absolute values, particularly in respect to the measurement error/noise. The difference is small enough to have been undetectable with other methods used in previous studies. We have amended the sentence to clarify this.

It now reads: “Subtle decreases in EMA which may have been undetected in previous studies correspond to discernible increases in tendon stress. For instance, reducing EMA from 0.242 (mean minimum EMA of the slow group) to 0.206 (mean minimum EMA of the fast group) was associated with an increase in tendon stress from ~50 MPa to ~60 MPa, decreasing safety factor from 2 to 1.67 (where 1 indicates failure), which is both measurable and physiologically significant.” (Line 195-200)

Lines 243-245: "The consistent net work observed among all speeds suggests the ankle extensors are performing similar amounts of ankle work independent of speed." If this is true, and presumably there is greater limb work performed on the center of mass at faster speeds (Donelan, Kram, Kuo), do more proximal leg joints increase work and energy consumption at faster speeds?

The skin over the proximal leg joints (knee and hip) moves too much to get reliable measures of EMA from the ratio of moment arms. This will be pursued in future work when all muscles are incorporated in the model so knee and hip EMA can be determined from muscle force.

We have added limitations and considerations paragraph to the manuscript: “Finally, we did not determine whether the EMA of proximal hindlimb joints (which are more difficult to track via surface motion capture markers) remained constant with speed. Although the hip and knee contribute substantially less work than the ankle joint (Fig. 4), the majority of kangaroo skeletal muscle is located around these proximal joints. A change in EMA at the hip or knee could influence a larger muscle mass than at the ankle, potentially counteracting or enhancing energy savings in the ankle extensor muscle-tendon units. Further research is needed to understand how posture and muscles throughout the whole body contribute to kangaroo energetics.” (Line 321-328)

Lines 245-246: "Previous studies using sonomicrometry have shown that the muscles of tammar wallabies do not shorten considerably during hops, but rather act near-isometrically as a strut" Which muscles? All muscles? Extensors at a single joint?

Added "gastrocnemius and plantaris" Line 164-165

Lines 249-254: "The cost of generating force hypothesis suggests that faster movement speeds require greater rates of muscle force development, and in turn greater cross-bridge cycling rates, driving up metabolic costs (Taylor et al. 1980, Kram and Taylor 1990). The ability for the ankle extensor muscle fibres to remain isometric and produce similar amounts of work at all speeds may help explain why hopping macropods do not follow the energetic trends observed in quadrupedal species." These sentences confuse me. Kram & Taylor's cost of force-generating hypothesis assumes that producing the same average force over shorter contact times increases metabolic rate. How does 'similar muscle work' across all speeds explain the ability of macropods to use unique energetic trends in the cost of force-generating hypothesis context?

Thank you for highlighting this confusion. We have substantially revised the discussion clarify where the mechanisms presented deviate from the cost of generating force hypothesis. Lines 270-309

Reviewer #3 (Recommendations For The Authors):

In addition to the points described in the public review, I have additional, related, specific comments:

(1) Results: Please refer to the hypotheses in the results, and relate the the findings back to the hypotheses.

We now relate the findings back to the hypotheses 

Line 142 “In partial support of hypothesis (i), greater masses and faster speeds were associated with more crouched hindlimb postures (Fig. 3a,c).”.

Lines 205-206: “The increase in tendon stress with speed, facilitated in part by the change in moment arms by the shift in posture, may explain changes in ankle work (c.f. Hypothesis (ii)).” 

(2) Results: please provide the main statistical results either in-line or in a table in the main text.

We (the co-authors) have discussed this at length, and have agreed that the manuscript is far more readable in the format whereby most statistics lie within the supplementary tables, otherwise a reader is met with a wall of statistics. We only include values in the main text when the magnitude is relevant to the arguments presented in the results and discussion.

(3) Line 140: Describe how 'crouched' was defined.

We have now added a brief definition of ‘Crouch factor’ after the figure caption. (Line 143) (Fig. 3a,c; where crouch factor is the ratio of total limb length to pelvis to toe distance).

(4) Line 162: This seems to be a main finding and should be a figure in the main text not supplemental. Additionally, Supplementary Figures 3a and b do not show this finding convincingly There should be a figure plotting r vs speed and r vs mass.

The combination of r and R are represented in the EMA plot in the main text. The r and R plots are relegated to the supplementary because the main text is already very crowded.  Thank you for the suggestion for the figure plotting r and R versus speed, this is now included as Suppl. Fig. 3h

(5) Line 166: Supplementary Figure 3g does not show the range of dorsiflexion angles as a function of speed. It shows r vs dorsiflexion angle. Please correct.

Thanks for noticing this, it was supposed to reference Fig 3g rather than Suppl Fig 3g in the sentence regarding speed. We have fixed this, Line 170. 

We had added a reference to Suppl Fig 3 on Line 169 as this shows where the peak in r with ankle angle occurs (114.4 degrees).

(6) Line 184: Where are the statistical results for this statement?

The relationship between stress and EMA does not appear to be linear, thus we only present R^{^}2 for the power relationship rather than a p-value. 

(7) Line 192: The authors should explain how joint work and power relate/support the overall hypotheses. This section also refers to Figures 4 and 5 even though Figures 6 and 7 have already been described. Please reorganize.

We have added a sentence at the end of the work and power section to mention hypothesis (ii) and lead into the discussion where it is elaborated upon. 

“The increase in positive and negative ankle work may be due to the increase in tendon stress rather than additional muscle work.” Line 219-220 We have rearranged the figure order.

(8) The statistics are not reported in the main text, but in the supplementary tables. If a result is reported in the main text, please report either in-line or with a table in the main text.

We leave most statistics in the supplementary tables to preserve the readability of the manuscript. We only include values in the main text when the magnitude is relevant to the arguments raised in the results and discussion.

Author response:

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

Reviewer #1 (Public review):

Summary:

This paper presents results from four independent experiments, each of which tests for rhythmicity in auditory perception. The authors report rhythmic fluctuations in discrimination performance at frequencies between 2 and 6 Hz. The exact frequency depends on the ear and experimental paradigm, although some frequencies seem to be more common than others.

Strengths:

The first sentence in the abstract describes the state of the art perfectly: "Numerous studies advocate for a rhythmic mode of perception; however, the evidence in the context of auditory perception remains inconsistent". This is precisely why the data from the present study is so valuable. This is probably the study with the highest sample size (total of > 100 in 4 experiments) in the field. The analysis is very thorough and transparent, due to the comparison of several statistical approaches and simulations of their sensitivity. Each of the experiments differs from the others in a clearly defined experimental parameter, and the authors test how this impacts auditory rhythmicity, measured in pitch discrimination performance (accuracy, sensitivity, bias) of a target presented at various delays after noise onset.

Weaknesses:

(1) The authors find that the frequency of auditory perception changes between experiments. I think they could exploit differences between experiments better to interpret and understand the obtained results. These differences are very well described in the Introduction, but don't seem to be used for the interpretation of results. For instance, what does it mean if perceptual frequency changes from between- to within-trial pitch discrimination? Why did the authors choose this experimental manipulation? Based on differences between experiments, is there any systematic pattern in the results that allows conclusions about the roles of different frequencies? I think the Discussion would benefit from an extension to cover this aspect.

We believe that interpreting these differences remains difficult and a precise, detailed (and possibly mechanistic) interpretation is beyond the goal of the present study. The main goal of this study was to explore the consistency and variability of effects across variations of the experimental design and samples of participants. Interpreting specific effects, e.g. at particular frequencies, would make sense mostly if differences between experiments have been confirmed in a separate reproduction. Still, we do provide specific arguments for why differences in the outcome between different experiments, e.g. with and without explicit trial initialization by the participants, could be expected. See lines 91ff in the introduction and 786ff in the discussion.

(2) The Results give the impression of clear-cut differences in relevant frequencies between experiments (e.g., 2 Hz in Experiment 1, 6 Hz in Exp 2, etc), but they might not be so different. For instance, a 6 Hz effect is also visible in Experiment 1, but it just does not reach conventional significance. The average across the three experiments is therefore very useful, and also seems to suggest that differences between experiments are not very pronounced (otherwise the average would not produce clear peaks in the spectrum). I suggest making this point clearer in the text.

We have revised the conclusions to note that the present data do not support clear cut differences between experiments. For this reason we also refrain from detailed interpretations of specific effects, as suggested by this reviewer in point 1 above.

(3) I struggle to understand the hypothesis that rhythmic sampling differs between ears. In most everyday scenarios, the same sounds arrive at both ears, and the time difference between the two is too small to play a role for the frequencies tested. If both ears operate at different frequencies, the effects of the rhythm on overall perception would then often cancel out. But if this is the case, why would the two ears have different rhythms to begin with? This could be described in more detail.

This hypothesis was not invented by us, but in essence put forward in previous work. The study by Ho et al. CurrBiol 2017 has reported rhythmic effects at different frequencies in the left and right ears, and we here tried to reproduce these effects. One could speculate about an ear-difference based on studies reporting a right-ear advantage in specific listening tasks, and the idea that different time scales of rhythmic brain activity may be specifically prevail in the left and right cortical hemispheres; hence it does not seem improbable that there could be rhythmic effects in both ears at different frequencies. We note this in the introduction, l. 65ff.

Reviewer #2 (Public review):

Summary:

The current study aims to shed light on why previous work on perceptual rhythmicity has led to inconsistent results. They propose that the differences may stem from conceptual and methodological issues. In a series of experiments, the current study reports perceptual rhythmicity in different frequency bands that differ between different ear stimulations and behavioral measures.

The study suggests challenges regarding the idea of universal perceptual rhythmicity in hearing.

Strengths:

The study aims to address differences observed in previous studies about perceptual rhythmicity. This is important and timely because the existing literature provides quite inconsistent findings. Several experiments were conducted to assess perceptual rhythmicity in hearing from different angles. The authors use sophisticated approaches to address the research questions.

Weaknesses:

(1) Conceptional concerns:

The authors place their research in the context of a rhythmic mode of perception. They also discuss continuous vs rhythmic mode processing. Their study further follows a design that seems to be based on paradigms that assume a recent phase in neural oscillations that subsequently influence perception (e.g., Fiebelkorn et al.; Landau & Fries). In my view, these are different facets in the neural oscillation research space that require a bit more nuanced separation. Continuous mode processing is associated with vigilance tasks (work by Schroeder and Lakatos; reduction of low frequency oscillations and sustained gamma activity), whereas the authors of this study seem to link it to hearing tasks specifically (e.g., line 694). Rhythmic mode processing is associated with rhythmic stimulation by which neural oscillations entrain and influence perception (also, Schroeder and Lakatos; greater low-frequency fluctuations and more rhythmic gamma activity). The current study mirrors the continuous rather than the rhythmic mode (i.e., there was no rhythmic stimulation), but even the former seems not fully fitting, because trials are 1.8 s short and do not really reflect a vigilance task. Finally, previous paradigms on phase-resetting reflect more closely the design of the current study (i.e., different times of a target stimulus relative to the reset of an oscillation). This is the work by Fiebelkorn et al., Landau & Fries, and others, which do not seem to be cited here, which I find surprising. Moreover, the authors would want to discuss the role of the background noise in resetting the phase of an oscillation, and the role of the fixation cross also possibly resetting the phase of an oscillation. Regardless, the conceptional mixture of all these facets makes interpretations really challenging. The phase-reset nature of the paradigm is not (or not well) explained, and the discussion mixes the different concepts and approaches. I recommend that the authors frame their work more clearly in the context of these different concepts (affecting large portions of the manuscript).

Indeed, the paradigms used here and in many similar previous studies incorporate an aspect of phase-resetting, as the presentation of a background noisy may effectively reset ongoing auditory cortical processes. Studies trying to probe for rhythmicity in auditory perception in the absence any background noise have not shown any effect (Zoefel and Heil, 2013), perhaps because the necessary rhythmic processes along auditory pathways are only engaged when some sound is present. We now discuss these points, and also acknowledge the mentioned studies in the visual system; l. 57.

(2) Methodological concerns:

The authors use a relatively unorthodox approach to statistical testing. I understand that they try to capture and characterize the sensitivity of the different analysis approaches to rhythmic behavioral effects. However, it is a bit unclear what meaningful effects are in the study. For example, the bootstrapping approach that identifies the percentage of significant variations of sample selections is rather descriptive (Figures 5-7). The authors seem to suggest that 50% of the samples are meaningful (given the dashed line in the figure), even though this is rarely reached in any of the analyses. Perhaps >80% of samples should show a significant effect to be meaningful (at least to my subjective mind). To me, the low percentage rather suggests that there is not too much meaningful rhythmicity present. 

We note that there is no clear consensus on what fraction of experiments should be expected or how this way of quantifying effects should be precisely valued (l. 441ff). However, we now also clearly acknowledge in the discussion that the effective prevalence is not very high (l. 663).

I suggest that the authors also present more traditional, perhaps multi-level, analyses: Calculation of spectra, binning, or single-trial analysis for each participant and condition, and the respective calculation of the surrogate data analysis, and then comparison of the surrogate data to the original data on the second (participant) level using t-tests. I also thought the statistical approach undertaken here could have been a bit more clearly/didactically described as well.

We here realize that our description of the methods was possibly not fully clear. We do follow the strategy as suggested by this reviewer, but rather than comparing actual and surrogate data based on a parametric t-test, we compare these based on a non-parametric percentile-based approach. This has the advantage of not making specific (and possibly not-warranted) assumptions about the distribution of the data. We have revised the methods to clarify this, l. 332ff. 

The authors used an adaptive procedure during the experimental blocks such that the stimulus intensity was adjusted throughout. In practice, this can be a disadvantage relative to keeping the intensity constant throughout, because, on average, correct trials will be associated with a higher intensity than incorrect trials, potentially making observations of perceptual rhythmicity more challenging. The authors would want to discuss this potential issue. Intensity adjustments could perhaps contribute to the observed rhythmicity effects. Perhaps the rhythmicity of the stimulus intensity could be analyzed as well. In any case, the adaptive procedure may add variance to the data.

We have added an analysis of task difficulty to the results (new section “Effects of adaptive task difficulty“) to address this. Overall we do not find systematic changes in task difficulty across participants for most of the experiments, but for sure one cannot rule out that this aspect of the design also affects the outcomes.  Importantly, we relied on an adaptive task difficulty to actually (or hopefully) reduce variance in the data, by keeping the task-difficulty around a certain level. Give the large number of trials collected, not using such an adaptive produce may result in performance levels around chance or near ceiling, which would make impossible to detect rhythmic variations in behavior. 

Additional methodological concerns relate to Figure 8. Figures 8A and C seem to indicate that a baseline correction for a very short time window was calculated (I could not find anything about this in the methods section). The data seem very variable and artificially constrained in the baseline time window. It was unclear what the reader might take from Figure 8.

This figure was intended mostly for illustration of the eye tracking data, but we agree that there is no specific key insight to be taken from this. We removed this. 

Motivation and discussion of eye-movement/pupillometry and motor activity: The dual task paradigm of Experiment 4 and the reasons for assessing eye metrics in the current study could have been better motivated. The experiment somehow does not fit in very well. There is recent evidence that eye movements decrease during effortful tasks (e.g., Contadini-Wright et al. 2023 J Neurosci; Herrmann & Ryan 2024 J Cog Neurosci), which appears to contradict the results presented in the current study. Moreover, by appealing to active sensing frameworks, the authors suggest that active movements can facilitate listening outcomes (line 677; they should provide a reference for this claim), but it is unclear how this would relate to eye movements. Certainly, a person may move their head closer to a sound source in the presence of competing sound to increase the signal-to-noise ratio, but this is not really the active movements that are measured here. A more detailed discussion may be important. The authors further frame the difference between Experiments 1 and 2 as being related to participants' motor activity. However, there are other factors that could explain differences between experiments. Self-paced trials give participants the opportunity to rest more (inter-trial durations were likely longer in Experiment 2), perhaps affecting attentional engagement. I think a more nuanced discussion may be warranted.

We expanded the motivation of why self-pacing trials may effectively alter how rhythmic processes affect perception, and now also allude to attention and expectation related effects (l. 786ff). Regarding eye movements we now discuss the results in the light of the previously mentioned studies, but again refrain from a very detailed and mechanistic interpretation (l. 782).

Discussion:

The main data in Figure 3 showed little rhythmicity. The authors seem to glance over this fact by simply stating that the same phase is not necessary for their statistical analysis. Previous work, however, showed rhythmicity in the across-participant average (e.g., Fiebelkorn's and similar work). Moreover, one would expect that some of the effects in the low-frequency band (e.g., 2-4 Hz) are somewhat similar across participants. Conduction delays in the auditory system are much smaller than the 0.25-0.5 s associated with 2-4 Hz. The authors would want to discuss why different participants would express so vastly different phases that the across-participant average does not show any rhythmicity, and what this would mean neurophysiologically.

We now discussion the assumptions and implications of similar or distinct phases of rhythmic processes within and between participants (l. 695ff). In particular we note that different origins of the underlying neurophysiological processes eventually may suggest that such assumptions are or a not warranted.  

An additional point that may require more nuanced discussion is related to the rhythmicity of response bias versus sensitivity. The authors could discuss what the rhythmicity of these different measures in different frequency bands means, with respect to underlying neural oscillations.

We expanded discussion to interpret what rhythmic changes in each of the behavioral metric could imply (l. 706ff).

Figures:

Much of the text in the figures seems really small. Perhaps the authors would want to ensure it is readable even for those with low vision abilities. Moreover, Figure 1A is not as intuitive as it could be and may perhaps be made clearer. I also suggest the authors discuss a bit more the potential monoaural vs binaural issues, because the perceptual rhythmicity is much slower than any conduction delays in the auditory system that could lead to interference.

We tried to improve the font sizes where possible, and discuss the potential monaural origins as suggested by other reviewers. 

Reviewer #3 (Public review):

Summary:

The finding of rhythmic activity in the brain has, for a long time, engendered the theory of rhythmic modes of perception, that humans might oscillate between improved and worse perception depending on states of our internal systems. However, experiments looking for such modes have resulted in conflicting findings, particularly in those where the stimulus itself is not rhythmic. This paper seeks to take a comprehensive look at the effect and various experimental parameters which might generate these competing findings: in particular, the presentation of the stimulus to one ear or the other, the relevance of motor involvement, attentional demands, and memory: each of which are revealed to effect the consistency of this rhythmicity.

The need the paper attempts to resolve is a critical one for the field. However, as presented, I remain unconvinced that the data would not be better interpreted as showing no consistent rhythmic mode effect. It lacks a conceptual framework to understand why effects might be consistent in each ear but at different frequencies and only for some tasks with slight variants, some affecting sensitivity and some affecting bias.

Strengths:

The paper is strong in its experimental protocol and its comprehensive analysis, which seeks to compare effects across several analysis types and slight experiment changes to investigate which parameters could affect the presence or absence of an effect of rhythmicity. The prescribed nature of its hypotheses and its manner of setting out to test them is very clear, which allows for a straightforward assessment of its results

Weaknesses:

There is a weakness throughout the paper in terms of establishing a conceptual framework both for the source of "rhythmic modes" and for the interpretation of the results. Before understanding the data on this matter, it would be useful to discuss why one would posit such a theory to begin with. From a perceptual side, rhythmic modes of processing in the absence of rhythmic stimuli would not appear to provide any benefit to processing. From a biological or homeostatic argument, it's unclear why we would expect such fluctuations to occur in such a narrow-band way when neither the stimulus nor the neurobiological circuits require it.

We believe that the framework for why there may be rhythmic activity along auditory pathways that shapes behavioral outcomes has been laid out in many previous studies, prominently here (Schroeder et al., 2008; Schroeder and Lakatos, 2009; Obleser and Kayser, 2019). Many of the relevant studies are cited in the introduction, which is already rather long given the many points covered in this study. 

Secondly, for the analysis to detect a "rhythmic mode", it must assume that the phase of fluctuations across an experiment (i.e., whether fluctuations are in an up-state or down-state at onset) is constant at stimulus onset, whereas most oscillations do not have such a total phase-reset as a result of input. Therefore, some theoretical positing of what kind of mechanism could generate this fluctuation is critical toward understanding whether the analysis is well-suited to the studied mechanism.

In line with this and previous comments (by reviewer 2) we have expanded the discussion to consider the issue of phase alignment (l. 695ff). 

Thirdly, an interpretation of why we should expect left and right ears to have distinct frequency ranges of fluctuations is required. There are a large number of statistical tests in this paper, and it's not clear how multiple comparisons are controlled for, apart from experiment 4 (which specifies B&H false discovery rate). As such, one critical method to identify whether the results are not the result of noise or sample-specific biases is the plausibility of the finding. On its face, maintaining distinct frequencies of perception in each ear does not fit an obvious conceptual framework.

Again this point was also noted by another reviewer and we expanded the introduction and discussion in this regard (l. 65ff).

Reviewer #1 (Recommendations for the authors):

(1) An update of the AR-surrogate method has recently been published (https://doi.org/10.1101/2024.08.22.609278). I appreciate that this is a lot of work, and it is of coursee up to the authors, but given the higher sensitivity of this method, it might be worth applying it to the four datasets described here.

Reading this article we note that our implementation of the AR-surrogate method was essentially as suggested here, and not as implemented by Brookshire. In fact we had not realized that Brookshire had apparently computed the spectrum based on the group-average data. As explained in the Methods section, as now clarified even better, we compute for each participant the actual spectrum of this participant’s data, and a set of surrogate spectra. We then perform a group-average of both to compute the p-value of the actual group-average based on the percentile of the distribution of surrogate averages. This send step differs from Harris & Beale, which used a one-sided t-test. The latter is most likely not appropriate in a strict statistical sense, but possibly more powerful for detecting true results compared to the percentile-based approach that we used (see l. 332ff).

(2) When results for the four experiments are reported, a reminder for the reader of how these experiments differ from each other would be useful.

We have added this in the Results section.

"considerable prevalence of differences around 4Hz, with dual‐task requirements leading to stronger rhythmicity in perceptual sensitivity". There is a striking similarity to recently published data (https://doi.org/10.1101/2024.08.10.607439 ) demonstrating a 4-Hz rhythm in auditory divided attention (rather than between modalities as in the present case). This could be a useful addition to the paragraph.

We have added a reference to this preprint, and additional previous work pointing in the same direction mentioned in there.  

(3) There are two typos in the Introduction: "related by different from the question", and below, there is one "presented" too much.

These have been fixed.

Reviewer #3 (Recommendations for the authors):

My major suggestion is that these results must be replicated in a new sample. I understand this is not simple to do and not always possible, but at this point, no effect is replicated from one experiment to the next, despite very small changes in protocol (especially experiment 1 vs 2). It's therefore very difficult to justify explaining the different effects as real as opposed to random effects of this particular sample. While the bootstrapping effects show the level of consistency of the effect within the sample studied, it can not be a substitute for a true replication of the results in a new sample.

We agree that only an independent replication can demonstrate the robustness of the results. We do consider experiment 1 a replication test of Ho et al. CurrBiol 2017, which results in different results than reported there. But more importantly, we consider the analysis of ‘reproducibility’ by simulating participant samples a key novelty of the present work, and want to emphasize this over the within-study replication of the same experiment.  In fact, in light of the present interpretation of the data, even a within-study replication would most likely not offer a clear-cut answer. 

As I said in the public review, the interpretation of the results, and of why perceptual cycles in arhythmic stimuli could be a plausible theory to begin with, is lacking. A conceptual framework would vastly improve the impact and understanding of the results.

We tried to strengthen the conceptual framework in the introduction. We believe that this is in large provided by previous work, and the aim of the present study was to explore the robustness of effects and not to suggest and discover novel effects. 

Minor comments:

(1) The authors adapt the difficulty as a function of performance, which seems to me a strange choice for an experiment that is analyzing the differences in performance across the experiment. Could you add a sentence to discuss the motivation for this choice?

We now mention the rationale in the Methods section and in a new section of the Results. There we also provide additional analyses on this parameter.

(2) The choice to plot the p-values as opposed to the values of the actual analysis feels ill-advised to me. It invites comparison across analyses that isn't necessarily fair. It would be more informative to plot the respective analysis outputs (spectral power, regression, or delta R2) and highlight the windows of significance and their overlap across analyses. In my opinion, this would be more fair and accurate depiction of the analyses as they are meant to be used.

We do disagree. As explained in the Methods (l. 374ff): “(Showing p-values) … allows presenting the results on a scale that can be directly compared between analysis approaches, metrics, frequencies and analyses focusing on individual ears or the combined data. Each approach has a different statistical sensitivity, and the underlying effect sizes (e.g. spectral power) vary with frequency for both the actual data and null distribution. As a result, the effect size reaching statistical significance varies with frequency, metrics and analyses.” 

The fact that the level of power (or R2 or whatever metric we consider) required to reach significance differs between analyses (one ear, both ears), metrics (d-prime, bias, RT) and between analyses approaches makes showing the results difficult, as we would need a separate panel for each of those. This would multiply the number of panels required e.g. for Figure 4 by 3, making it a figure with 81 axes. Also neither the original quantities of each analysis (e.g. spectral power) nor the p-values that we show constitute a proper measure of effect size in a statistical sense. In that sense, neither of these is truly ideal for comparing between analyses, metrics etc. 

We do agree thought that many readers may want to see the original quantification and thresholds for statistical significance. We now show these in an exemplary manner for the Binned analysis of Experiment 1, which provides a positive result and also is an attempt to replicate the findings by  Ho et al 2017. This is shown in new Figure 5. 

(3) Typo in line 555 (+ should be plus minus).

(4) Typo in line 572: "Comparison of 572 blocks with minus dual task those without"

(5) Typo in line 616: remove "one".

(6) Line 666 refers to effects in alpha band activity, but it's unclear what the relationship is to the authors' findings, which peak around 6 Hz, lower than alpha (~10 Hz).

(7) Line 688 typo, remove "amount of".

These points have been addressed.  

(8) Oculomotor effect that drives greater rhythmicity at 3-4 Hz. Did the authors analyze the eye movements to see if saccades were also occurring at this rate? It would be useful to know if the 3-4 Hz effect is driven by "internal circuitry" in the auditory system or by the typical rate of eye movement.

A preliminary analysis of eye movement data was in previous Figure 8, which was removed on the recommendation of another review.  This showed that the average saccade rate is about 0.01 saccade /per trial per time bin, amounting to on average less than one detected saccade per trial. Hence rhythmicity in saccades is unlikely to explain rhythmicity in behavioral data at the scale of 34Hz. We now note this in the Results.

Obleser J, Kayser C (2019) Neural Entrainment and Attentional Selection in the Listening Brain. Trends Cogn Sci 23:913-926.

Schroeder CE, Lakatos P (2009) Low-frequency neuronal oscillations as instruments of sensory selection. Trends Neurosci 32:9-18.

Schroeder CE, Lakatos P, Kajikawa Y, Partan S, Puce A (2008) Neuronal oscillations and visual amplification of speech. Trends Cogn Sci 12:106-113.

Zoefel B, Heil P (2013) Detection of Near-Threshold Sounds is Independent of EEG Phase in Common Frequency Bands. Front Psychol 4:262.

Author response:

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

Reviewer #1 (Public review):

Summary:

This is an interesting study characterizing and engineering so-called bathy phytochromes, i.e., those that respond to near infrared (NIR) light in the ground state, for optogenetic control of bacterial gene expression. Previously, the authors have developed a structure-guided approach to functionally link several light-responsive protein domains to the signaling domain of the histidine kinase FixL, which ultimately controls gene expression. Here, the authors use the same strategy to link bathy phytochrome light-responsive domains to FixL, resulting in sensors of NIR light. Interestingly, they also link these bathy phytochrome light-sensing domains to signaling domains from the tetrathionate-sensing SHK TtrS and the toluene-sensing SHK TodS, demonstrating the generality of their protein engineering approach more broadly across bacterial two-component systems.

This is an exciting result that should inspire future bacterial sensor design. They go on to leverage this result to develop what is, to my knowledge, the first system for orthogonally controlling the expression of two separate genes in the same cell with NIR and Red light, a valuable contribution to the field.

Finally, the authors reveal new details of the pH-dependent photocycle of bathy phytochromes and demonstrate that their sensors work in the gut - and plant-relevant strains E. coli Nissle 1917 and A. tumefaciens.

Strengths:

(1) The experiments are well-founded, well-executed, and rigorous.

(2) The manuscript is clearly written.

(3) The sensors developed exhibit large responses to light, making them valuable tools for ontogenetic applications.

(4) This study is a valuable contribution to photobiology and optogenetics.

We thank the reviewer for the positive verdict on our manuscript.

Weaknesses:

(1) As the authors note, the sensors are relatively insensitive to NIR light due to the rapid dark reversion process in bathy phytochromes. Though NIR light is generally non-phototoxic, one would expect this characteristic to be a limitation in some downstream applications where light intensities are not high (e.g., in vivo).

We principally concur with this reviewer’s assessment that delivery of light (of any color) into living tissue can be severely limited by absorption, reflection, and scattering. That notwithstanding, at least two considerations suggest that in-vivo deployment of the pNIRusk setups we presently advance may be feasible.

First, while the pNIRusk setups are indeed less light-sensitive compared to, e.g., our earlier redlight-responsive pREDusk and pDERusk setups (see Meier et al. Nat Commun 2024), we note that the overall light fluences required for triggering them are in the range of tens of µW per cm₂. By contrast, optogenetic experiments in vivo, in particular in the neurosciences, often employ light area intensities on the order of mW per cm₂ and above. Put another way, compared to the optogenetic tools used in these experiments, the pNIRusk setups are actually quite sensitive to light.

Second, sensitivity to NIR light brings the advantage of superior tissue penetration, see data reported by Weissleder Nat Biotech 2001 and Ash et al. Lasers Med Sci 2017 (both papers are cited in our manuscript). Based on these data, the intensity of blue light (450 nm) therefore falls off 5-10 times more strongly with penetration depth than that of NIR light (800 nm).

We have added a brief treatment of these aspects in the Discussion section.

(2) Though they can be multiplexed with Red light sensors, these bathy phytochrome NIR sensors are more difficult to multiplex with other commonly used light sensors (e.g., blue) due to the broad light responsivity of the Pfr state. This challenge may be overcome by careful dosing of blue light, as the authors discuss, but other bacterial NIR sensing systems with less cross-talk may be preferred in some applications.

The reviewer is correct in noting that, at least to a certain extent, the pNIRusk systems also respond to blue light owing to their Soret absorbance bands (see Fig. 1). That said, we note two points:

First, a given photoreceptor that preferentially responds to certain wavelengths, e.g., 700 nm in the case of conventional bacterial phytochromes (BphP), generally absorbs shorter wavelengths to some degree as well. Absorption of these shorter wavelengths suffices for driving electronic and/or vibronic transitions of the chromophore to higher energy levels which often give rise to productive photochemistry and downstream signal transduction. Put another way, a certain response of sensory photoreceptors to shorter wavelengths is hence fully expected and indeed experimentally borne out, as for instance shown by Ochoa-Fernandez et al. in the so-called PULSE setup (Nat Meth 2020, doi: 10.1038/s41592-020-0868-y).

Second, known BphPs share similar Pr and Pfr absorbance spectra. We therefore expect other BphP-based optogenetic setups to also respond to blue light to some degree. Currently, there are insufficient data to gauge whether individual BphPs systematically differ in their relative sensitivity to blue compared to red or NIR light. Arguably, pertinent experiments may be an interesting subject for future study.

Reviewer #2 (Public review):

Summary:

In this manuscript, Meier et al. engineer a new class of light-regulated two-component systems. These systems are built using bathy-bacteriophytochromes that respond to near-infrared (NIR) light. Through a combination of genetic engineering and systematic linker optimization, the authors generate bacterial strains capable of selective and tunable gene expression in response to NIR stimulation. Overall, these results are an interesting expansion of the optogenetic toolkit into the NIR range. The cross-species functionality of the system, modularity, and orthogonality have the potential to make these tools useful for a range of applications.

Strengths:

(1) The authors introduce a novel class of near-infrared light-responsive two-component systems in bacteria, expanding the optogenetic toolbox into this spectral range.

(2) Through engineering and linker optimization, the authors achieve specific and tunable gene expression, with minimal cross-activation from red light in some cases.

(3) The authors show that the engineered systems function robustly in multiple bacterial strains, including laboratory E. coli, the probiotic E. coli Nissle 1917, and Agrobacterium tumefaciens.

(4) The combination of orthogonal two-component systems can allow for simultaneous and independent control of multiple gene expression pathways using different wavelengths of light.

(5) The authors explore the photophysical properties of the photosensors, investigating how environmental factors such as pH influence light sensitivity.

Weaknesses:

(1) The expression of multi-gene operons and fluorescent reporters could impose a metabolic burden. The authors should present data comparing optical density for growth curves of engineered strains versus the corresponding empty-vector control to provide insight into the burden and overall impact of the system on host viability and growth.

In response to this comment, we have recorded growth kinetics of bacteria harboring the pNIRusk-DsRed plasmids or empty vectors under both inducing (i.e., under NIR light) and noninducing conditions (i.e., darkness). We did not observe systematic differences in the growth kinetics between the different cultures, thus suggesting that under the conditions tested there is no adverse effect on cell viability.

We include the new data in Suppl. Fig. 5c-d and refer to them in the main text.

(2) The manuscript consistently presents normalized fluorescence values, but the method of normalization is not clear (Figure 2 caption describes normalizing to the maximal fluorescence, but the maximum fluorescence of what?). The authors should provide a more detailed explanation of how the raw fluorescence data were processed. In addition, or potentially in exchange for the current presentation, the authors should include the raw fluorescence values in supplementary materials to help readers assess the actual magnitude of the reported responses.

We appreciate this valid comment and have altered the representation of the fluorescence data. All values for a given fluorescent protein (i.e., either DsRed or YPet) across all systems are now normalized to a single reference value, thus enabling direct comparison between experiments.

(3) Related to the prior point, it would be useful to have a positive control for fluorescence that could be used to compare results across different figure panels.

As all data are now normalized to the same reference value, direct comparison across all figures is enabled.

(4) Real-time gene expression data are not presented in the current manuscript, but it would be helpful to include a time-course for some of the key designs to help readers assess the speed of response to NIR light.

In response to this comment, we include in the revised manuscript induction kinetics of bacterial cultures bearing pNIRusk upon transfer to inducing NIR-light conditions. To this end, aliquots were taken at discrete timepoints, transcriptionally and translationally arrested, and analyzed for optical density and DsRed reporter fluorescence after allowing for chromophore maturation.

We include the new data in Suppl. Fig. 5e and refer to them in the manuscript.

Moreover, we note that the experiments in Agrobacterium tumefaciens used a luciferase reporter thus enabling the continuous monitoring of the light-induced expression kinetics. These data (unchanged in revision) are to be found in Suppl. Fig. 9.

Reviewer #3 (Public review):

Summary:

This paper by Meier et al introduces a new optogenetic module for the regulation of bacterial gene expression based on "bathy-BphP" proteins. Their paper begins with a careful characterization of kinetics and pH dependence of a few family members, followed by extensive engineering to produce infrared-regulated transcriptional systems based on the authors' previous design of the pDusk and pDERusk systems, and closing with characterization of the systems in bacterial species relevant for biotechnology.

Strengths:

The paper is important from the perspective of fundamental protein characterization, since bathyBphPs are relatively poorly characterized compared to their phytochrome and cyanobacteriochrome cousins. It is also important from a technology development perspective: the optogenetic toolbox currently lacks infrared-stimulated transcriptional systems. Infrared light offers two major advantages: it can be multiplexed with additional tools, and it can penetrate into deep tissues with ease relative to the more widely used blue light-activated systems. The experiments are performed carefully, and the manuscript is well written.

Weaknesses:

My major criticism is that some information is difficult to obtain, and some data is presented with limited interpretation, making it difficult to obtain intuition for why certain responses are observed. For example, the changes in red/infrared responses across different figures and cellular contexts are reported but not rationalized. Extensive experiments with variable linker sequences were performed, but the rationale for linker choices was not clearly explained. These are minor weaknesses in an overall very strong paper.

We are grateful for the positive take on our manuscript.

Reviewer #1 (Recommendations for the authors):

(1) As eLife is a broad audience journal, please define the Soret and Q-bands (line 125).

We concur and have added labels in fig. 1a that designate the Soret and Q bands.

(2) The initial (0) Ac design in Figure 2b is activated by NIR and Red light, albeit modestly. The authors state that this construct shows "constant reporter fluorescence, largely independent of illumination" (line 167). This language should be changed to reflect the fact that this Ac construct responds to both of these wavelengths.

Agreed. We have amended the text accordingly.

(3) pNIRusk Ac 0 appears to show a greater light response than pNIRusk Av -5. However, the authors claim that the former is not light-responsive and the latter is. This conclusion should be explained or changed.

The assignment of pNIRusk Av-5 as light-responsive is based on the relative difference in reporter fluorescence between darkness and illumination with either red or NIR light. Although the overall fluorescence is much lower in Av-5 than for Av-0, the relative change upon illumination is much more pronounced. We add a statement to this effect to the text.

(4) The authors state that "when combining DmDERusk-Str-YPet with AvTod+21-DsRed expression rose under red and NIR light, respectively, whereas the joint application of both light colors induced both reporter genes" (lines 258-261). In contrast, Figure 3c shows that application of both wavelengths of light results in exclusive activation of YPet expression. It appears the description of the data is wrong and must be corrected. That said, this error does not impact their conclusion that two separate target genes can be independently activated by NIR and red light.

We thank the reviewer for catching this error which we have corrected in the revised manuscript.

(5) Line 278: I don't agree with the authors' blanket statement that the use of upconversion nanoparticles is a "grave" limitation for NIR-light mediated activation of bacterial gene expression in vivo. The authors should either expound on the severity of the limitation or use more moderate language.

We have replaced the word ‘grave’ by ‘potential’ and thereby toned down our wording.

Reviewer #2 (Recommendations for the authors):

(1) Please include a discussion on the expected depth penetration of different light wavelengths. This is most relevant in the context of the discussion about how these NIR systems could be used with living therapeutics.

Given the heterogeneity of biological tissue, it is challenging to state precise penetration depths for different wavelengths of light. That said, blue light for instance is typically attenuated by biological tissue around 5 to 10 times as strongly as near-infrared light is.

We have expanded the Discussion chapter to cover these aspects.

(2) It would be helpful for Figure 2C (or supplementary) to also include the response to blue light stimulation.

We agree and have acquired pertinent data for the blue-light response. The new data are included in an updated Fig. 2c. Data acquired at varying NIR-light intensities, originally included in Fig. 2c, have been moved to Suppl. Fig. 5a-b.

(3) In Figure 4A, data on the response of E. coli Nissle to blue and red light are missing. Including this would help identify whether the reduced sensitivity to non-NIR wavelengths observed in the E. coli lab strain is preserved in the probiotic background.

In response to this comment, we have acquired pertinent data on E. coli Nissle. While the results were overall similar to those in the laboratory strain, the response to blue and NIR light was yet lower in the Nissle bacteria which stands to benefit optogenetic applications.

We have updated Fig. 4a accordingly. For clarity, we only show the data for AvNIRusk in the main paper but have relegated the data on AcNIRusk to Suppl. Fig. 8. (Note that this has necessitated a renumbering of the subsequent Suppl. Figs.)

(4) On many of the figures, there are thin gray lines that appear between the panels that it would be nice to eliminate because, in some cases, they cut through words and numbers.

The grey lines likely arose from embedding the figures into the text document. In the typeset manuscript, which has become available on the eLife webpage in the meantime, there are no such lines. That said, we will carefully check throughout the submission/publishing/proofing process lest these lines reappear.

(5) Page 7, line 155: "As not least seen" typo or awkward phrasing.

We have restructured the sentence and thereby hopefully clarified the unclear phrasing.

(6) Page 7, line 167: It does not appear to be the case that the initial pNIRusk designs show constant fluorescence that is largely independent of illumination. AcNIRusk shows an almost twofold change from dark to NIR. Reword this to avoid confusion.

We concur with this comment, similar to reviewer #1’s remark, and have adjusted the text accordingly.

(7) Page 8, line 174: Related to the previous point, AvNIRusk has one design that is very minimally light switchable (-5), so stating that six light switchable designs have been identified is also confusing.

As stated in our response to reviewer #1 above, the assignment of AvNIRusk-5 as light-switchable is based on the relative fluorescence change upon illumination. We have added an explanation to the text.

(8) Page 10, line 228-229: I was not able to find the data showing that expression levels were higher for the DmTtr systems than the pREDusk and pNIRusk setups. This may be an issue related to the normalization point. It was not clear to me how to compare these values.

We apologize for the initially unclear representation of the data. In response to this reviewer’s general comments above, we have now normalized all fluorescence values to a single reference value, thus allowing their direct comparison.

(9) Page 12, line 264: "finer-grained expression control can be exerted..." Either show data or adjust the language so that it is clear this is a prediction.

True, we have replaced ‘can’ by ‘could’.

(10) Page 25, line 590: CmpX13 cells have a reference that is given later, but it should be added where it first appears.

Agreed, we have added the reference in the indicated place.

(11) Page 25, line 592: define LB/Kan.

We had already defined this abbreviation further up but, for clarity, we have added it again in the indicated position.

(12) Page 40, line 946: "normalized by" rather than "to".

We have implemented the requested change in the indicated and several other positions of the manuscript.

(13) Figures 2C, 3C, and similar plots in the supplementary material would benefit from having a legend for the colors.

We agree and have added pertinent legends to the corresponding main and supplementary figures.

(14) As a reader, I had some trouble following all the acronyms. This is at the author's discretion, but I would eliminate ones that are not strictly essential (e.g. MTP for microtiter plate; I was unable to identify what "MCS" meant; look for other opportunities to remove acronyms).

In the revised manuscript, we have defined the abbreviation ‘MCS’ (for ‘multiple-cloning site’) upon first occurrence. We have decided to retain the abbreviation ‘MTP’ in the text.

(15) Could the authors briefly speculate on why A. tumefaciens activation with red light might occur?

While we can but speculate as to the underlying reasons for the divergent red-light response in A. tumefaciens, we discuss possible scenarios below.

Commonly, two-component systems (TCS) exhibit highly cooperative and steep responses to signal. As a consequence, even small differences in the intracellular amounts of phosphorylated and unphosphorylated response regulator (RR) can give to significantly changed gene-expression output. Put another way, the gene-expression output need not scale linearly with the extent of RR phosphorylation but, rather, is expected to show nonlinear dependence with pronounced thresholding effects.

Differences in the pertinent RR levels can for instance arise from variations in the expression levels of the pNIRusk system components between E. coli and A. tumefaciens. Moreover, the two bacteria greatly differ in their two-component-system (TCS) repertoire. Although TCSs are commonly well insulated from each other, cross-talk with endogenous TCSs, even if limited, may cause changes in the levels of phosphorylated RR and hence gene-expression output. In a similar vein, the RR can also be phosphorylated and dephosphorylated non-enzymatically, e.g., by reaction with high-energy anhydrides (such as acetyl phosphate) and hydrolysis, respectively. Other potential origins for the divergent red-light response include differences in the strength of the promoters driving expression of the pNIRusk system components and the fluorescent/luminescent reporters, respectively.

(16) It would be helpful for the authors to briefly explain why they needed to switch to luminescence from fluorescence for the A. tumeraciens studies.

While there was no strict necessity to switch from the fluorescence-based system used in E. coli to a luminescence-based system in A. tumefaciens, we opted for luminescence based on prior experience with other Alphaproteobacteria (e.g., 10.1128/mSystems.00893-21), where luminescence offered significant advantages. Specifically, it provides essentially background-free signal detection and greater sensitivity for monitoring gene expression. In addition, as demonstrated in Suppl. Fig. 9c and d, the luminescence system enables real-time tracking of gene expression dynamics, which further supported its use in our experimental setup (see our response to reviewer #2’s general comments).

(17) This is a very minor comment that the authors can take or leave, but I got hung up on the word "implement" when it appeared a few times in the manuscript because I tended to read it as "put a plan into place" rather than its other meaning.

In the abstract, we have replaced one instance of the word ‘implement’ by ‘instrument’.

(18) The authors should include the relevant constructs on AddGene or another public strainsharing service.

We whole-heartedly subscribe to the idea of freely sharing research materials with fellow scientists. Therefore, we had already deposited the most relevant AvNIRusk in Addgene, even prior to the initial submission of the manuscript (accession number 235084). In the meantime, we have released the deposition, and the plasmid can be obtained from Addgene since May 15_th of this year.

Reviewer #3 (Recommendations for the authors):

Suggestion for improvement:

This paper relies heavily on variations in linker sequences to shift responses. I am familiar with prior work from the Moglich lab in which helical linkers were employed to shift responses in synthetic two-component systems, with interesting periodicity in responses with every 7 residues (as expected for an alpha helix) and inversion of responses at smaller linker shifts. There is no mention in this paper whether their current engineering follows a similar rationale, what types of linkers are employed (e.g. flexible vs helical), and whether there is an interpretation for how linker lengths alter responses. Can you explain what classes of linker sequences are used throughout Figures 2 and 3, and whether length or periodicity affects the outcome? This would be very helpful for readers who are new to this approach, or if the rationale here differs from the authors' prior work.

The PATCHY approach employed at present followed a closely similar rationale as in our previous studies. That is, linkers were extended/shortened and varied in their sequence by recombining different fragments of the natural linkers of the parental receptors, i.e., the bacteriophytochrome and the FixL sensor histidine kinase, respectively. We have added a statement to this effect in the text and a reference to Suppl. Fig. 3 which illustrates the principal approach.

Compared to our earlier studies, we isolated fewer receptor variants supporting light-regulated responses, despite covering a larger sequence space. Owing to the sparsity of the light-regulated variants, an interpretation of the linker properties and their correlation with light-regulated activity is challenging. Although doubtless unsatisfying from a mechanistic viewpoint, we therefore refrain from a pertinent discussion which would be premature and speculative at this point. As the reviewer raises a valid and important point, we have expanded the text by referring to our earlier studies and the observed dependence of functional properties on linker composition.

It is sometimes difficult to intuit or rationalize the differences in red/IR sensitivity across closely related variants. An important example appears in Figure 3C vs 3B. I think the AvTod+21 in 3B should be the equivalent to the DsRed response in the second column of 3C (AvTod+21 + DmDERusk), except, of course, that the bacteria in 3C carry an additional plasmid for the DERusk system. However, in 3B, the response to red light is substantial - ~50% as strong as that for IR, whereas in 3C, red light elicits no response at all. What is the difference? The reason this is important is that the AvTod+21 and DMDERusk represent the best "orthogonal" red and infrared light responses, but this is not at all obvious from 3B, where AvTod+21 still causes a substantial (and for orthogonality, undesirable) response under red light. Perhaps subtle differences in expression level due to plasmid changes cause these differences in light responses? Could the authors test how the expression level affects these responses? The paper would be greatly improved if observations of the diverse red/IR responses could be rationalized by some design criteria.

As noted above in our response to reviewer #2, we have now normalized all fluorescence readings to joint reference values, thus allowing a better comparison across experiments.

The reviewer is correct in noting that upon multiplexing, the individual plasmid systems support lower fluorescence levels than when used in isolation. We speculate that the combination of two plasmids may affect their copy numbers (despite the use of different resistance markers and origins of replications) and hence their performance. Likewise, the cellular metabolism may be affected when multiple plasmids are combined. These aspects may well account for the absent red-light response in AvTod+21 in the multiplexing experiments which is – indeed – unexpected. As, at present, we cannot provide a clear rationalization for this effect, we recommend verifying the performance of the plasmid setups when multiplexing.

The paper uses "red" and "infrared" to refer to ~624 nm and ~800 nm light, respectively. I wonder whether it might be possible to shift these peak wavelengths to obtain even better separation for the multiplexing experiments. Perhaps shifting the specific red wavelength could result in better separation between DERusk and AvTod systems, for example? Could the authors comment on this (maybe based on action spectra of their previously developed tools) or perhaps test a few additional stimulation wavelengths?

The choice of illumination wavelengths used in these experiments is dictated by the LED setups available for illumination of microtiter plates. On the one hand, we are using an SMD (surface-mount device) three-color LED with a fixed wavelength of the red channel around 624 nm (see Hennemann et al., 2018). On the other hand, we are deploying a custom-built device with LEDs emitting at around 800 nm (see Stüven et al., 2019 and this work). Adjusting these wavelengths is therefore challenging, although without doubt potentially interesting.

To address this reviewer comment, we have added a statement to the text that the excitation wavelengths may be varied to improve multiplexed applications.

Additional minor comments:

(1) Figure 2C: It would be very helpful to place a legend on the figure panel for what the colors indicate, since they are unique to this panel and non-intuitive.

This comment coincides with one by reviewer #2, and we have added pertinent legends to this and related supplementary figures.

(2) Figure 3C: it is not obvious which system uses DsRed and which uses YPet in each combination, since the text indicates that all combinations were cloned, and this is not clearly described in the legend. Is it always the first construct in the figure legend listed for DsRed and the second for YPet?

For clarification, we have revised the x-axis labels in Fig. 3C. (And yes, it is as this reviewer surmises: the first of the two constructs harbored DsRed and the second one YPet.)

Author response:

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

Reviewer #1 (Public Review):

This is an interesting study of the nature of representations across the visual field. The question of how peripheral vision differs from foveal vision is a fascinating and important one. The majority of our visual field is extra-foveal yet our sensory and perceptual capabilities decline in pronounced and well-documented ways away from the fovea. Part of the decline is thought to be due to spatial averaging (’pooling’) of features. Here, the authors contrast two models of such feature pooling with human judgments of image content. They use much larger visual stimuli than in most previous studies, and some sophisticated image synthesis methods to tease apart the prediction of the distinct models.

More importantly, in so doing, the researchers thoroughly explore the general approach of probing visual representations through metamers-stimuli that are physically distinct but perceptually indistinguishable. The work is embedded within a rigorous and general mathematical framework for expressing equivalence classes of images and how visual representations influence these. They describe how image-computable models can be used to make predictions about metamers, which can then be compared to make inferences about the underlying sensory representations. The main merit of the work lies in providing a formal framework for reasoning about metamers and their implications, for comparing models of sensory processing in terms of the metamers that they predict, and for mapping such models onto physiology. Importantly, they also consider the limits of what can be inferred about sensory processing from metamers derived from different models.

Overall, the work is of a very high standard and represents a significant advance over our current understanding of perceptual representations of image structure at different locations across the visual field. The authors do a good job of capturing the limits of their approach and I particularly appreciated the detailed and thoughtful Discussion section and the suggestion to extend the metamer-based approach described in the MS with observer models. The work will have an impact on researchers studying many different aspects of visual function including texture perception, crowding, natural image statistics, and the physiology of low- and mid-level vision.

The main weaknesses of the original submission relate to the writing. A clearer motivation could have been provided for the specific models that they consider, and the text could have been written in a more didactic and easy-to-follow manner. The authors could also have been more explicit about the assumptions that they make.

Thank you for the summary. We appreciate the positives noted above. We address the weaknesses point by point below.

Reviewer #2 (Public Review):

Summary

This paper expands on the literature on spatial metamers, evaluating different aspects of spatial metamers including the effect of different models and initialization conditions, as well as the relationship between metamers of the human visual system and metamers for a model. The authors conduct psychophysics experiments testing variations of metamer synthesis parameters including type of target image, scaling factor, and initialization parameters, and also compare two different metamer models (luminance vs energy). An additional contribution is doing this for a field of view larger than has been explored previously

General Comments

Overall, this paper addresses some important outstanding questions regarding comparing original to synthesized images in metamer experiments and begins to explore the effect of noise vs image seed on the resulting syntheses. While the paper tests some model classes that could be better motivated, and the results are not particularly groundbreaking, the contributions are convincing and undoubtedly important to the field. The paper includes an interesting Voronoi-like schematic of how to think about perceptual metamers, which I found helpful, but for which I do have some questions and suggestions. I also have some major concerns regarding incomplete psychophysical methodology including lack of eye-tracking, results inferred from a single subject, and a huge number of trials. I have only minor typographical criticisms and suggestions to improve clarity. The authors also use very good data reproducibility practices.

Thank you for the summary. We appreciate the positives noted above. We address the weaknesses point by point below.

Specific Comments

Experimental Setup

Firstly, the experiments do not appear to utilize an eye tracker to monitor fixation. Without eye tracking or another manipulation to ensure fixation, we cannot ensure the subjects were fixating the center of the image, and viewing the metamer as intended. While the short stimulus time (200ms) can help minimize eye movements, this does not guarantee that subjects began the trial with correct fixation, especially in such a long experiment. While Covid-19 did at one point limit in-person eye-tracked experiments, the paper reports no such restrictions that would have made the addition of eye-tracking impossible. While such a large-scale experiment may be difficult to repeat with the addition of eye tracking, the paper would be greatly improved with, at a minimum, an explanation as to why eye tracking was not included.

Addressed on pg. 25, starting on line 658.

Secondly, many of the comparisons later in the paper (Figures 9,10) are made from a single subject. N=1 is not typically accepted as sufficient to draw conclusions in such a psychophysics experiment. Again, if there were restrictions limiting this it should be discussed. Also (P11) Is subject sub-00 is this an author? Other expert? A naive subject? The subject’s expertise in viewing metamers will likely affect their performance.

Addressed on pg. 14, starting on line 308.

Finally, the number of trials per subject is quite large. 13,000 over 9 sessions is much larger than most human experiments in this area. The reason for this should be justified.

In general, we needed a large number of trials to fit full psychometric functions for stimuli derived for both models, with both types of comparison, both initializations, and over many target images. We could have eliminated some of these, but feel that having a consistent dataset across all these conditions is a strength of the paper.

In addition to the sentence on pg. 14, line 318, a full enumeration of trials is now described on pg. 23, starting on line 580.

Model

For the main experiment, the authors compare the results of two models: a ’luminance model’ that spatially pools mean luminance values, and an ’energy model’ that spatially pools energy calculated from a multi-scale pyramid decomposition. They show that these models create metamers that result in different thresholds for human performance, and therefore different critical scaling parameters, with the basic luminance pooling model producing a scaling factor 1/4 that of the energy model. While this is certain to be true, due to the luminance model being so much simpler, the motivation for the simple luminance-based model as a comparison is unclear.

The use of simple models is now addressed on pg. 3, starting on line 98, as well as the sentence starting on pg. 4 line 148: the luminance model is intended as the simplest possible pooling model.

The authors claim that this luminance model captures the response of retinal ganglion cells, often modeled as a center-surround operation (Rodieck, 1964). I am unclear in what aspect(s) the authors claim these center-surround neurons mimic a simple mean luminance, especially in the context of evidence supporting a much more complex role of RGCs in vision (Atick & Redlich, 1992). Why do the authors not compare the energy model to a model that captures center-surround responses instead? Do the authors mean to claim that the luminance model captures only the pooling aspects of an RGC model? This is particularly confusing as Figures 6 and 9 show the luminance and energy models for original vs synth aligning with the scaling of Midget and Parasol RGCs, respectively. These claims should be more clearly stated, and citations included to motivate this. Similarly, with the energy model, the physiological evidence is very loosely connected to the model discussed.

We have removed the bars showing potential scaling values measured by electrophysiology in the primate visual system and attempted to clarify our language around the relationship between these models and physiology. Our metamer models are only loosely connected to the physiology, and we’ve decided in revision not to imply any direct connection between the model parameters and physiological measurements. The models should instead be understood as loosely inspired by physiology, but not as a tool to localize the representation (as was done in the Freeman paper).

The physiological scaling values are still used as the mean of the priors on the critical scaling value for model fitting, as described on pg. 27, starting on line 698.

Prior Work:

While the explorations in this paper clearly have value, it does not present any particularly groundbreaking results, and those reported are consistent with previous literature.The explorations around critical eccentricity measurement have been done for texture models (Figure 11) in multiple papers (Freeman 2011, Wallis, 2019, Balas 2009). In particular, Freeman 20111 demonstrated that simpler models, representing measurements presumed to occur earlier in visual processing need smaller pooling regions to achieve metamerism. This work’s measurements for the simpler models tested here are consistent with those results, though the model details are different. In addition, Brown, 2023 (which is miscited) also used an extended field of view (though not as large as in this work). Both Brown 2023, and Wallis 2019 performed an exploration of the effect of the target image. Also, much of the more recent previous work uses color images, while the author’s exploration is only done for greyscale.

We were pleased to find consistency of our results with previous studies, given the (many) differences in stimuli and experimental conditions (especially viewing angle), while also extending to new results with the luminance model, and the effects of initialization. Note that only one of the previous studies (Freeman and Simoncelli, 2011) used a pooled spectral energy model. Moreover, of the previous studies, only one (Brown et al., 2023) used color images (we have corrected that citation - thanks for catching the error).

Discussion of Prior Work:

The prior work on testing metamerism between original vs. synthesized and synthesized vs. synthesized images is presented in a misleading way. Wallis et al.’s prior work on this should not be a minor remark in the post-experiment discussion. Rather, it was surely a motivation for the experiment. The text should make this clear; a discussion of Wallis et al. should appear at the start of that section. The authors similarly cite much of the most relevant literature in this area as a minor remark at the end of the introduction (P3L72).

The large differences we observed between comparison types (original vs synthesized, compared to synthesized vs synthesized) surprised us. Understanding such difference was not a primary motivation for the work, but it is certainly an important component of our results. In the introduction, we thought it best to lay out the basic logic of the metamer paradigm for foveated vision before mentioning the complications that are introduced in both the Wallis and Brown papers (paragraph beginning p. 3, line 109). Our results confirm and bolster the results of both of those earlier works, which are now discussed more fully in the Introduction (lines 109 and following).

White Noise: The authors make an analogy to the inability of humans to distinguish samples of white noise. It is unclear however that human difficulty distinguishing samples of white noise is a perceptual issue- It could instead perhaps be due to cognitive/memory limitations. If one concentrates on an individual patch one can usually tell apart two samples. Support for these difficulties emerging from perceptual limitations, or a discussion of the possibility of these limitations being more cognitive should be discussed, or a different analogy employed.

We now note the possibility of cognitive limits on pg. 8, starting on line 243, as well as pg. 22, line 571. The ability of observers to distinguish samples of white noise is highly dependent on display conditions. A small patch of noise (i.e., large pixels, not too many) can be distinguished, but a larger patch cannot, especially when presented in the periphery. This is more generally true for textures (as shown in Ziemba and Simoncelli (2021)). Samples of white noise at the resolution used in our study are indistinguishable.

Relatedly, in Figure 14, the authors do not explain why the white noise seeds would be more likely to produce syntheses that end up in different human equivalence classes.

In figure 14, we claim that white noise seeds are more likely to end up in the same human equivalence classes than natural image seeds. The explanation as to why we think this may be the case is now addressed on pg. 19, starting on line 423.

It would be nice to see the effect of pink noise seeds, which mirror the power spectrum of natural images, but do not contain the same structure as natural images - this may address the artifacts noted in Figure 9b.

The lack of pink noise seeds is now addressed on pg. 19, starting on line 429.

Finally, the authors note high-frequency artifacts in Figure 4 & P5L135, that remain after syntheses from the luminance model. They hypothesize that this is due to a lack of constraints on frequencies above that defined by the pooling region size. Could these be addressed with a white noise image seed that is pre-blurred with a low pass filter removing the frequencies above the spatial frequency constrained at the given eccentricity?

The explanation for this is similar to the lack of pink noise seeds in the previous point: the goal of metamer synthesis is model testing, and so for a given model, we want to find model metamers that result in the smallest possible critical scaling value. Taking white noise seed images and blurring them will almost certainly remove the high frequencies visible in luminance metamers in figure 4 and thus result in a larger critical scaling value, as the reviewer points out. However, the logic of the experiments requires finding the smallest critical scaling value, and so these model metamers would be uninformative. In an early stage of the project, we did indeed synthesize model metamers using pink noise seeds, and observed that the high frequency artifacts were less prominent.

Schematic of metamerism: Figures 1,2,12, and 13 show a visual schematic of the state space of images, and their relationship to both model and human metamers. This is depicted as a Voronoi diagram, with individual images near the center of each shape, and other images that fall at different locations within the same cell producing the same human visual system response. I felt this conceptualization was helpful. However, implicitly it seems to make a distinction between metamerism and JND (just noticeable difference). I felt this would be better made explicit. In the case of JND, neighboring points, despite having different visual system responses, might not be distinguishable to a human observer.

Thanks for noting this – in general, metamers are subthreshold, and for the purpose of the diagram, we had to discretize the space showing metameric regions (Voronoi regions) around a set of stimuli. We’ve rewritten the captions to explain this better. We address the binary subthreshold nature of the metamer paradigm in the discussion section (pg. 19, line 438).

In these diagrams and throughout the paper, the phrase ’visual stimulus’ rather than ’image’ would improve clarity, because the location of the stimulus in relation to the fovea matters whereas the image can be interpreted as the pixels displayed on the computer.

We agree and have tried to make this change, describing this choice on pg. 3 line 73.

Other

The authors show good reproducibility practices with links to relevant code, datasets, and figures.

Reviewer #1 (Recommendations For The Authors):

In its current form, I found the introduction to be too cursory. I felt that the article would benefit from a clearer motivation for the two models that are considered as the reader is left unclear why these particular models are of special scientific significance. The luminance model is intended to capture some aspects of retinal ganglion cells response characteristics and the spectral energy model is intended to capture some aspects of the primary visual cortex. However, one can easily imagine models that include the pooling of other kinds of features, and it would be helpful to get an idea of why these are not considered. Which aspects of processing in the retina and V1 are being considered and which are being left out, and why? Why not consider representations that capture even higher-order statistical structure than those covered by the spectral energy model (or even semantics)? I think a bit of rewriting with this in mind could improve the introduction.

Along similar lines, I would have appreciated having the logic of the study explained more explicitly and didactically: which overarching research question is being asked, how it is operationalised in the models and experiments, and what are the predictions of the different models. Figures 2 and 3 are certainly helpful, but I felt further explanations would have made it easier for the reader to follow. Throughout, the writing could be improved by a careful re-reading with a view to making it easier to understand. For example, where results are presented, a sentence or two expanding on the implications would be helpful.

I think the authors could also be more explicit about the assumptions they make. While these are obviously (tacitly) included in the description of the models themselves, it would be helpful to state them more openly. To give one example, when introducing the notion of critical scaling, on p.6 the authors state as if it is a self-evident fact that "metamers can be achieved with windows whose size is matched to that of the underlying visual neurons". This presumably is true only under particular conditions, or when specific assumptions about readout from populations of neurons are invoked. It would be good to identify and state such assumptions more directly (this is partly covered in the Discussion section ’The linking proposition underlying the metamer paradigm’, but this should be anticipated or moved earlier in the text).

We agree that our introduction was too cursory and have reworked it. We have also backed off of the direct comparison to physiology and clarified that we chose these two as the simplest possible pooling models. We have also added sentences at the end of each result section attempting to summarize the implication (before discussing them fully in the discussion). Hopefully the logic and assumptions are now clearer.

There are also some findings that warrant a more extensive discussion. For example, what is the broader implication of the finding that original vs. synthesised and synthesised vs. synthesised comparisons exhibit very different scaling values? Does this tell us something about internal visual representations, or is it simply capturing something about the stimuli?

We believe this difference is a result of the stimuli that are used in the experiment and thus the synthesis procedure itself, which interacts with the model’s pooled image feature. We have attempted to update the relevant figures and discussions to clarify this, in the sections starting on pg 17 line 396 and pg. 19 line 417.

At some points in the paper, a third model (’texture model’) creeps into the discussion, without much explanation. I assume that this refers to models that consider joint (rather than marginal) statistics of wavelet responses, as in the famous Portilla & Simoncelli texture model. However, it would be helpful to the reader if the authors could explain this.

Addressed on pg. 3, starting on line 94.

Minor corrections.

Caption of Figure 3: ’top’ and ’bottom’ should be ’left’ and ’right’

Line 177: ’smallest tested scaling values tested’. Remove one instance of ’tested’

Line 212: ’the images-specific psychometric functions’ -> ’image-specific’

Line 215: ’cloud-like pink noise’. It’s not literally pink noise, so I would drop this.

Line 236: ’Importantly, these results cannot be predicted from the model, which gives no specific insight as to why some pairs are more discriminable than others’. The authors should specify what we do learn from the model if it fails to provide insight into why some image pairs are more discriminable than others.

Figure 9: it might be helpful to include small insets with the ’highway’ and ’tiles’ source images to aid the reader in understanding how the images in 9B were generated.

Table 1 placement should be after it is first referred to on line 258.

In the Discussion section "Why does critical scaling depend on the comparison being performed", it would be helpful to consider the case where the two model metamers *are* distinguishable from each other even though each is indistinguishable from the target image. I would assume that this is possible (e.g., if the target image is at the midpoint between the two model images in image space and each of the stimuli is just below 1 JND away from the target). Or is this not possible for some reason?

Regarding line 236: this specific line has been removed, and the discussion about this issue has all been consolidated in the final section of the discussion, starting on pg. 19 line 438.

Regarding the final comment: this is addressed in the paragraph starting on pg. 16 line 386. To expand upon that: the situation laid out by the reviewer is not possible in our conceptualization, in which metamerism is transitive and image discriminability is binary. In order to investigate situations like the one laid out by the reviewer, one needs models whose representations have metric properties, i.e., which allow you to measure and reason about perceptual distance, which we refer to in the paragraph starting on pg. 20 line 460. We also note that this situation has not been observed in this or any other pooling model metamer study that we are aware of. All other minor changes have been addressed.

Reviewer #2 (Recommendations For The Authors):

Original image T should be marked in the Voronoi diagrams.

Brown et al is miscited as 2021 should be ACM Transactions on Applied Perception 2023.

Figure 3 caption: models are left and right, not top and bottom.

Thanks, all of the above have been addressed.

References

BrownReral Encoding, in the Human Visual System. ACM Transactions on Applied Perception. 2023 Jan; 20(1):1–22.http://dx.doi.org/10.1145/356460, Dutell V, Walter B, Rosenholtz R, Shirley P, McGuire M, Luebke D. Efficient Dataflow Modeling of Periph-5, doi: 10.1145/3564605.

Freeman Jdoi: 10.1038/nn.2889, Simoncelli EP. Metamers of the ventral stream. Nature Neuroscience. 2011 aug; 14(9):1195–1201..

Ziemba CMnications. 2021 jul; 12(1)., Simoncelli EP. Opposing Effects of Selectivity and Invariance in Peripheral Vision. Nature Commu-https://doi.org/10.1038/s41467-021-24880-5, doi: 10.1038/s41467-021-24880-5.

Author response:

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

Reviewer #1 (Public Review):

(1) The authors make fairly strong claims that "arousal-related fluctuations are isolated from neurons in the deep layers of the SC" (emphasis added). This conclusion is based on comparisons between a "slow drift axis", a low-dimensional representation of neuronal drift, and other measures of arousal (Figures 2C, 3) and motor output sensitivity (Figures 2B, 3B). However, the metrics used to compare the slow-drift axis and motor activity were computed during separate task epochs: the delay period (600-1100 ms) and a perisaccade epoch (25 ms before and after saccade initiation), respectively. As the authors reference, deep-layer SC neurons are typically active only around the time of a saccade. Therefore, it is not clear if the lack of arousal-related modulations reported for deep-layer SC neurons is because those neurons are truly insensitive to those modulations, or if the modulations were not apparent because they were assessed in an epoch in which the neurons were not active. A potentially more valuable comparison would be to calculate a slow-drift axis aligned to saccade onset. 

The reviewer makes an important point that the calculation of an axis can depend critically on the time window of neuronal response. We find when considering this that the slow drift axis is less sensitive to this issue because it is calculated on time-averaged activity over multiple trials. In previous work we found that slow drift calculated on the stimulus evoked response in V4 was very well aligned to slow drift calculated on pre-stimulus spontaneous activity (Cowley et al, Neuron, 2020, Supplemental Figure 3A and 3B). To address this issue in the present data, we compared the axis computed for an example session for neural activity during the delay period and neural activity aligned to saccade onset. As shown new Figure 2 – figure supplement 1 in the revised manuscript, we found a similar lack of arousal-related modulations for deep-layer SC neurons when slow drift was computed using the saccade epoch (25ms before to 25ms after the onset of the saccade). Figure 2 – figure supplement 1A shows loadings for the SC slow drift axis when it was computed using spiking responses during the delay period (as in the main manuscript analysis). In contrast, Figure 2 – figure supplement 1B shows loadings from the same session when the SC slow drift axis was computed using spiking responses during the saccade epoch. The plots are highly similar and in both cases the loadings were weaker for neurons recorded from channels at the bottom of the probe which have a higher motor index. Finally, we found that projections onto the SC slow drift axis for this session were strongly correlated when the slow drift axis was computed using spiking responses during the delay period and the saccade epoch (r = 0.66, p < 0.001, Figure 1C). Taken together, these results suggest that arousal-related modulations are less evident in deep-layer SC neurons irrespective of whether slow drift was computed during the delay or saccade epoch (see also Public Reviews, Reviewer 1, Point 2).

(2) More generally, arousal-related signals may persist throughout multiple different epochs of the task. It would be worthwhile to determine whether similar "slow-drift" dynamics are observed for baseline, sensory-evoked, and saccade-related activity. Although it may not be possible to examine pupil responses during a saccade, there may be systematic relationships between baseline and evoked responses. 

Similar to the point above, slow drift dynamics tend to be similar across different response epochs because they are averaged across many trials and seem to tap into responsivity trends that are robust across epochs. As shown in Author response image 1 below, and the Figure 2 – figure supplement 1 in the revised manuscript, similar dynamics were observed when the SC slow drift axis was computed using spiking responses during the baseline, delay, visual and saccade epochs. We did not investigate differences between baseline and evoked pupil responses in the current paper. However, these effects were characterized in one of our previous papers that focused exclusively on the relationship between slow drift and eye-related metrics (Johnston et al., 2022, Cereb. Cortex, Figure 6). In this previous work, we found a negative correlation between baseline and evoked pupil size. Both variables were significantly correlated with slow drift, the only difference being the sign of the correlation.

Author response image 1.

(A-C) Dynamics of slow drift for three example sessions when the SC slow drift axis was computed using spiking responses during the baseline, delay, visual and saccade epochs. Baseline = 100ms before the onset of the target stimulus; Delay = 600 to 1100ms after the offset of the target stimulus; Stim = 25ms to 125ms after the onset of the target stimulus; Sac = 25ms before to 25ms after the onset of the saccade.

Johnston R, Snyder AC, Khanna SB, Issar D, Smith MA (2022) The eyes reflect an internal cognitive state hidden in the population activity of cortical neurons. Cereb Cortex 32:3331–3346.

(3) The relationships between changes in SC activity and pupil size are quite small (Figures 2C & 5C). Although the distribution across sessions (Figure 2C) is greater than chance, they are nearly 1/4 of the size compared to the PFC-SC axis comparisons. Likewise, the distribution of r2 values relating pupil size and spiking activity directly (Figure 5) is quite low. We remain skeptical that these drifts are truly due to arousal and cannot be accounted for by other factors. For example, does the relationship persist if accounting for a very simple, monotonic (e.g., linear) drift in pupil size and overall firing rate over the course of an individual session? 

Firstly, it is important to note that the strength of the relationship between projections onto the SC slow drift axis and pupil size (r² = 0.06) is within the range reported by Joshi et al. (2016, Neuron, Figure 3). They investigated the median variance explained between the spiking responses of individual SC neurons and pupil size and found it to be approximately 0.02 across sessions. Secondly, our statistical approach of testing the actual distribution of r² values against a shuffled distribution was specifically designed to rule out the possibility that the relationship between SC spiking responses and pupil size occurred due to linear drifts. The shuffled distribution in Figure 2C of the main manuscript represents the variance that can be explained by one session’s slow drift correlated with another session’s pupil, which would contain effects that occurred due to linear drifts alone. That the actual proportion of variance explained was significantly greater than this distribution suggests that the relationship between projections onto the SC slow drift axis and pupil size reflects changes in arousal rather than other factors related to linear drifts.

Joshi S, Li Y, Kalwani RM, Gold JI (2016) Relationships between Pupil Diameter and Neuronal Activity in the Locus Coeruleus, Colliculi, and Cingulate Cortex. Neuron 89:221–234.

(4) It is not clear how the final analysis (Figure 6) contributes to the authors' conclusions. The authors perform PCA on: (i) residual spiking responses during the delay period binned according to pupil size, and (ii) spiking responses in the saccade epoch binned according to target location (i.e., the saccade tuning curve). The corresponding PCs are the spike-pupil axis and the saccade tuning axis, respectively. Unsurprisingly, the spikepupil axis that captures variance associated with arousal (and removes variance associated with saccade direction) was not correlated with a saccade-tuning axis that captures variance associated with saccade direction and omits arousal. Had these measures been related it would imply a unique association between a neuron's preferred saccade direction and pupil control- which seems unlikely. The separation of these axes thus seems trivial and does not provide evidence of a "mechanism...in the SC to prevent arousal-related signals interfering with the motor output." It remains unknown whether, for example, arousal-related signals may impact trial-by-trial changes in neuronal gain near the time of a saccade, or alter saccade dynamics such as acceleration, precision, and reaction time. 

The reviewer makes a good point, and we agree that more evidence is needed to determine if the separation of the pupil size axis and saccade tuning axis is the mechanism through which cognitive and arousal-related signals can be intermixed in the SC. In the revised manuscript (lines 679-682), we have raised this as a possible explanation that necessitates further study rather than stating definitively that it is the exact mechanism through which these signals are kept separate. Our analysis here is similar to the one from Smoulder et al (2024, Neuron, Fig. 2F), in which the interactions between reward signals and target tuning in M1 were examined (and found to be orthogonal). While we agree with the reviewer that it may seem “trivial” for these axes to be orthogonal, it does not have to be so. If, for example, neural tuning curves shifted with changes in pupil size through gain changes that revealed tuning or affected tuning curve shape, there could be projections of the pupil axis onto the target tuning axis. Thus, while we agree with the reviewer that it appears sensible for these two axes to be orthogonal, our result is nonetheless a novel finding. We have edited the text in our revised manuscript, however, to make sure the nuance of this point is conveyed to the reader.

Smoulder AL, Marino PJ, Oby ER, Snyder SE, Miyata H, Pavlovsky NP, Bishop WE, Yu BM, Chase SM, Batista AP. A neural basis of choking under pressure. Neuron. 2024 Oct 23;112(20):3424-33.

Reviewer #2 (Public Review):

(1) The greatest weakness in the present research is the fact that arousal is a functionally less important non-motoric variable. The authors themselves introduce the problem with a discussion of attention, which is without any doubt the most important cognitive process that needs to be functionally isolated from oculomotor processes. Given this introduction, one cannot help but wonder, why the authors did not design an experiment, in which spatial attention and oculomotor control are differentiated. Absent such an experiment, the authors should spend more time explaining the importance of arousal and how it could interfere with oculomotor behavior. 

Although attention does represent an important cognitive process, we did not design an experiment in which attention and oculomotor control are differentiated because attention does not appear to be related to slow drift. In our first paper that reported on this phenomenon, we investigated the effects of spatial attention on slow fluctuations in neural activity by cueing the monkeys to attend to a stimulus in the left or right visual field in a block-wise manner. Each block lasted ~20 minutes and we found that slow drift did not covary with the timing of cued blocks (see Figure 4A, Cowley et al., 2020, Neuron). Furthermore, there is a large body of work showing that arousal also impacts motor behavior leading to changes in a range of eye-related metrics (e.g., pupil size, microsaccade rate and saccadic reaction time - for review, see Di Stasi et al. 2013, Neurosci. Biobehav. Rev.). We also note that the terms attention and arousal are often used in nonspecific and overlapping ways in the literature, adding to some potential confusion here. Nonetheless, pupil-linked arousal is an important variable that impacts motor performance. This has now been stated clearly in the Introduction of the revised manuscript (lines 108-114) to address the reviewer’s concerns and highlight the importance of studying how precise fixation and eye movements are maintained even in the presence of signals related to ongoing changes in brain state. 

Cowley BR, Snyder AC, Acar K, Williamson RC, Yu BM, Smith MA (2020) Slow Drift of Neural Activity as a Signature of Impulsivity in Macaque Visual and Prefrontal Cortex. Neuron 108:551-567.e8.

(2) In this context, it is particularly puzzling that one actually would expect effects of arousal on oculomotor behavior. Specifically, saccade reaction time, accuracy, and speed could be influenced by arousal. The authors should include an analysis of such effects. They should also discuss the absence or presence of such effects and how they affect their other results. 

As described above, several studies across species have demonstrated that arousal impacts motor behavior e.g., saccade reaction time, saccade velocity and microsaccade rate (for review, see Di Stasi et al. 2013, Neurosci. Biobehav. Rev.). This has been clarified in the Introduction of the revised manuscript to address the reviewer's concerns (lines 108-114). Our prior work (Johnston et al, Cerebral Cortex, 2022) shows that slow drift impacts several types of oculomotor behavior. Overall, these studies highlight the impact of arousal on eye movements as a robust effect, and support the present investigation into arousal and oculomotor control signals. While we agree reaction time, accuracy, and speed all can be influenced by arousal depending on task demands, the present study is focused on the connection between slow fluctuations in neural activity, linked to arousal, and different subpopulations of SC neurons. 

Di Stasi LL, Catena A, Cañas JJ, Macknik SL, Martinez-Conde S (2013) Saccadic velocity as an arousal index in naturalistic tasks. Neurosci Biobehav Rev 37:968–975.

Johnston R, Snyder AC, Khanna SB, Issar D, Smith MA (2022) The eyes reflect an internal cognitive state hidden in the population activity of cortical neurons. Cereb Cortex 32:3331–3346.

(3) The authors use the analysis shown in Figure 6D to argue that across recording sessions the activity components capturing variance in pupil size and saccade tuning are uncorrelated. however, the distribution (green) seems to be non-uniform with a peak at very low and very high correlation specifically. The authors should test if such an interpretation is correct. If yes, where are the low and high correlations respectively? Are there potentially two functional areas in SC? 

We agree with the reviewer that our actual data distribution was non-uniform. We examined individual sessions with high and low variance explained and did not find notable differences. One source of this variation has to do with session length. Longer sessions in principle should have a chance distribution of variance explained closer to zero because they contained more time bins. Given that we had no specific hypothesis for a non-uniform distribution, we have simply displayed the full distribution of values in our figure and the statistical result of a comparison to a shuffled distribution.

Reviewer #3 (Public Review):

(1) However, I am concerned about two main points: First, the authors repeatedly say that the "output" layers of the SC are the ones with the highest motor indices. This might not necessarily be accurate. For example, current thresholds for evoking saccades are lowest in the intermediate layers, and Mohler & Wurtz 1972 suggested that the output of the SC might be in the intermediate layers. Also, even if it were true that the high motor index neurons are the output, they are very few in the authors' data (this is also true in a lot of other labs, where it is less likely to see purely motor neurons in the SC). So, this makes one wonder if the electrode channels were simply too deep and already out of the SC? In other words, it seems important to show distributions of encountered neurons (regardless of the motor index) across depth, in order to better know how to interpret the tails of the distributions in the motor index histogram and in the other panels of Figure Supplement 1. I elaborate more on these points in the detailed comments below. 

The reviewer makes a good point about the efferent signals from SC. It is true that electrical thresholds are often lowest in intermediate layers, though deep layers do project to the oculomotor nuclei (Sparks, 1986; Sparks & Hartwich-Young, 1989) and often intermediate and deep layers are considered to function together to control eye movements (Wurtz & Albano, 1980). As suggested by the reviewer, we have edited the text throughout the manuscript to say that slow drift was less evident in SC neurons with a higher motor index, as well as included the above references and points about the intermediate and deep layers (Lines 73-81). Aside from the question of which layers of the SC function as the “motor output”, the reviewer raises a separate and important question – are our deep recordings still in SC. Here, we can say definitively that they are. We removed neurons if they did not exhibit elevated (above baseline) firing rates during the visual or saccade epochs of the MGS task (see Methods section on “Exclusion criteria”). All included neurons possessed a visual, visuomotor or motor response, consistent with the response properties of neurons in the SC. In addition, we found a number of neurons well above the bottom of the probe with strong motor responses and minimal loadings onto the slow drift axis (see Figure 2 – figure supplement 1A), consistent with the reviewer’s comment that intermediate layer neurons are tuned for movement and play a role in saccade production.

Mohler CW, Wurtz RH. Organization of monkey superior colliculus: intermediate layer cells discharging before eye movements. Journal of neurophysiology. 1976 Jul 1;39(4):722-44.

Sparks DL. Translation of sensory signals into commands for control of saccadic eye movements: role of primate superior colliculus. Physiol Rev. 1986 Jan;66(1):118-71. doi: 10.1152/physrev.1986.66.1.118. PMID: 3511480.

Sparks DL, Hartwich-Young R. The deep layers of the superior colliculus. Reviews of oculomotor research. 1989 Jan 1;3:213-55.

Wurtz RH, Albano JE. Visual-motor function of the primate superior colliculus. Annu Rev Neurosci. 1980;3:189-226. doi: 10.1146/annurev.ne.03.030180.001201. PMID: 6774653.

(2) Second, the authors find that the SC cells with a low motor index are modulated by pupil diameter. However, this could be completely independent of an "arousal signal". These cells have substantial visual responses. If the pupil diameter changes, then their activity should be influenced since the monkey is watching a luminous display. So, in this regard, the fact that they do not see "an arousal signal" in most motor neurons (through the pupil diameter analyses) is not evidence that the arousal signal is filtered out from the motor neurons. It could simply be that these neurons simply do not get affected by the pupil diameter because they do not have visual sensitivity. So, even with the pupil data, it is still a bit tricky for me to interpret that arousal signals are excluded from the "output layers" of the SC. 

The reviewer makes an important point about the SC’s visual responses. Neurons with a low motor index are, conversely, likely to have a stronger visual response index. However, we do not believe that changes in luminance can explain why the correlation between SC spiking response and pupil size is weaker for neurons with a lower motor index. Firstly, the changes in pupil size observed in the current paper and our previous work are slow and occur on a timescale of minutes (Cowley et al., 2020, Neuron) and are correlated with eye movement measures such as reaction time and microsaccade rate (Johnston et al., 2022, Cerebral Cortex). This is in stark contrast to luminance-evoked changes in pupil size that occur on a timescale of less than a second. Secondly, as shown the new Figure 5 – figure supplement 1 in the revised manuscript, very similar results were found when SC spiking responses were correlated with pupil size during the baseline period, when only the fixation point was on the screen. Although the luminance of the small peripheral target stimulus can result in small luminance-evoked changes in pupil size, no changes in luminance occurred during the baseline period which was defined as 100ms before the onset of the target stimulus. In Figure 2 – figure supplement 1 and Author response image 1 above, we show that slow drift is the same whether calculated on the baseline response, delay period, or peri-saccadic epoch. Thus, the measurement of slow drift is insensitive to the precise timing of the selection of both the window for the spiking response and the window for the pupil measurement. If luminance were the explanation for the slow changes in firing observed in visually responsive SC neurons, it would require those neurons to exhibit robust, sustained tuned responses to the small changes in retinal illuminance induced by the relatively small fluctuations in pupil size we observed from minute to minute. We are aware of no reports of such behavior in visually-responsive neurons in SC. We have included these analyses and this reasoning in the revised manuscript on lines 478-495.

Reviewer#1 (Recommendations for the author):

(1) It would be useful to provide line numbers in subsequent manuscripts for reviewers.

Line numbers have been added in the revised version of the manuscript.

(2) Page #6; last sentence: "...even impact processing at the early to mid stages of the visuomotor transformation, without leading to unwanted changes in motor output." I do not believe the authors have provided evidence that arousal levels were not associated with changes in motor output.

As suggested by Reviewer 3 (see Public Reviews, Reviewer 3, Point 2), we have edited the text throughout the manuscript to say that slow drift was less evident in SC neurons with a higher motor index. This sentence in the revised manuscript now reads:

“This provides a potential mechanism through which signals related to cognition and arousal can exist in the SC, and even impact processing at the early to mid stages of the visuomotor transformation, without leading to unwanted changes in SC neurons that are linked to saccade execution.”

(3) Page #8; last paragraph: Although deep-layer SC neurons may not have been obtained during every recording session, a summary of the motor index scores observed along the probe across sessions would be useful to confirm their assumptions. 

See Author response image 2 below which shows the motor index of each recoded SC neuron on the x-axis and session number on the y-axis. The points are colored by to the squared factor loading which represents the variance explained between the response a neuron and the slow drift axis (see Figure 3B of the main manuscript). You can see from this plot that neurons with a stronger component loading (shown in teal to yellow) typically have a lower motor index whereas the opposite is true for neurons with a weaker component loading (shown in dark blue).

Author response image 2.

Scatter plot showing the motor index of each recorded neuron along with the session number in which it was recorded. The points are colored by to the squared factor loading for each neuron along the slow drift axis. Note that loadings above 0.5 (33 data points in total) have been thresholded at 0.5 so that we could effectively use the color range to show all of the slow drift axis loadings.

(4) Page #10; first paragraph: The authors should state the time window of the delay period used, since it may be distinct from the pupil analysis (first 200ms of delay). 

This has been stated in the revised version of the manuscript. The sentence now reads:

“We first asked if arousal-related fluctuations are present in the SC. As in previous studies that recorded from neurons in the cortex (Cowley et al., 2020), we found that the mean spiking responses of individual SC neurons during the delay period (chosen at random on each trial from a uniform distribution spanning 600-1100ms, see Methods) fluctuated over the course of a session while the monkeys performed the MGS task (Figure 2A, left).”

(5) Page #10; second paragraph: Extra period at the end of a sentence: " most variance in the data..". 

Fixed in the revised version of the manuscript.

(6) Page #12: "between projections onto the SC slow drift axis and mean pupil size during the first 200ms of the delay period when a task-related pupil response could be observed." What criteria was used to determine whether a task-related pupil response was observed? 

This was chosen based on the results of a previous study in our lab that used the same memory-guided saccade task to investigate the relationship between slow drift and changes in based and evoked pupil size (see Johnston et al., 2022, Cereb. Cortex, Figure 6B). The period was chosen based on plotting the average pupil size aligned on different trial epochs. As we show in Figure 5-figure supplement 3 above, the pupil interactions with slow drift did not depend on the particular time window of the pupil we chose.  

(7) Page #14; Figure 2A: The axes for the individual channels are strangely floating and quite different from all other figures. Please label the channel in the figure legend that was used as an example of the projected values onto the slow drift axis.

The figure has been changed in the revised version of the manuscript so that the tick mark denoting zero residual spikes per second is on the top layer of each plot. A scale bar was chosen instead of individual axes to reduce clutter in the figure as it was used to demonstrate how slow drift was computed. Residual spiking responses from all neurons were projected on the slow drift axis to generate the scatter plot in the bottom right-hand corner of Figure 2A. There is no single neuron to label.

(8) Page #16: "These results demonstrate that even though arousal-related fluctuations are present in the SC, they are isolated from deep-layer neurons that elicit a strong saccadic response and presumably reside closer to the motor output." In line with our major comments, lack of arousal-related activity during the delay period is meaningless for deep-layer SC neurons that are generally inactive during this time. It does not imply that there is no arousal signal! 

Addressed in Public Reviews, Reviewer 1, Point 1 & 2. We found a similar lack of arousal-related modulations reported for deep-layer SC neurons when slow drift was computed using the saccade epoch (Figure 1 above). In addition, similar dynamics were observed when the SC slow drift axis was computed using spiking responses during the baseline, delay, visual and saccade period (Figure 2).

(9) Page #18: "These findings provide additional support for the hypothesis that arousalrelated fluctuations are isolated from neurons in the deep layers of the SC." The same criticism from above applies.

Addressed in Public Reviews, Reviewer 1, Point 1 & 2.

(10) Page #20; paragraph 3: "Taken together, the findings outlined above..." Would be useful to be more specific when referring to "activity" ; e.g., "...these neurons did not exhibit large fluctuations in delay-period activity over time".

This sentence has been changed in the revised manuscript in light of the reviewer’s comments. It now reads:

“In addition to being more weakly correlated with pupil size, the spiking responses of these neurons did not exhibit large fluctuations over time (Figure 2), and when considering the neuronal population as a whole, explained less variance in the slow drift axis when it was computed using population activity in the SC (Figure 3) and PFC (Figure 4).”

Reviewer #3 (Recommendations for the author):

The paper is clear and well-written. However, I am concerned about two main points: 

(1) First, the authors repeatedly say that the "output" layers of the SC are the ones with the highest motor indices. This might not necessarily be accurate. For example, current thresholds for evoking saccades are lowest in the intermediate layers, and Mohler & Wurtz 1972 suggested that the output of the SC might be in the intermediate layers. Also, even if it were true that the high motor index neurons are the output, they are very few in the authors' data (this is also true in a lot of other labs, where it is less likely to see purely motor neurons in the SC). So, this makes one wonder if the electrode channels were simply too deep and already out of the SC. In other words, it seems important to show distributions of encountered neurons (regardless of motor index) across depth, in order to better know how to interpret the tails of the distributions in the motor index histogram and in the other panels of the figure supplement 1. I elaborate more on these points in the detailed comments below. 

Addressed in Public Reviews, Reviewer 3, Point 1.

(2) Second, the authors find that the SC cells with a low motor index are modulated by pupil diameter. However, this could be completely independent of an "arousal signal". These cells have substantial visual responses. If the pupil diameter changes, then their activity should be influenced since the monkey is watching a luminous display. So, in this regard, the fact that they do not see "an arousal signal" in most motor neurons (through the pupil diameter analyses) is not evidence that the arousal signal is filtered out from the motor neurons. It could simply be that these neurons simply do not get affected by the pupil diameter because they do not have visual sensitivity. So, even with the pupil data, it is still a bit tricky for me to interpret that arousal signals are excluded from the "output layers" of the SC. 

Addressed in Public Reviews, Reviewer 3, Point 2.

(3) I think that a remedy to the first point above is to change the text to make it a bit more descriptive and less interpretive. For example, just say that the slow drifts were less evident among the neurons with high motor index. 

We thank the reviewer for this suggestion (see Public Reviews, Reviewer 3, Point 1).

(4) For the second point, I think that it is important to consider the alternative caveat of different amounts of light entering the system. Changes in light level caused by pupil diameter variations can be quite large. 

We thank the reviewer for this suggestion (see Public Reviews, Reviewer 3, Point 2).

(5) Line 31: I'm a bit underwhelmed by this kind of statement. i.e. we already know that cognitive processes and brain states do alter eye movements, so why is it "critical" that high precision fixation and eye movements are maintained? And, isn't the next sentence already nulling this idea of criticality because it does show that the brain state alters the SC neurons? In fact, cognitive processes are already known to be most prevalent in the intermediate and deep layers of the SC. 

It seems clear that while cognitive state does affect eye movements, it is desirable to have some separation between cognitive state and eye movement control. Covert attention, for instance, is precisely a situation where eye movement control is maintained to avoid overt saccades to the attended stimulus, and yet there are clear indications of attention’s impact on microsaccades and fixation. We stand by our statement that an important goal of vision is to have precise fixation and movements of the eye, and yet at the same time the eyes are subject to numerous influences by cognitive state.

(6) Line 65: it is better to clarify that these are "functional layers" because there are actually more anatomical layers. 

We have edited this sentence in the revised version of the manuscript so that it now reads:

“The role of these projections in the visuomotor transformation depends on the functional layer of the SC in which they terminate”.

(7) Line 73: this makes it sound like only the deepest layers are topographically organized, which is not true. Also, as early as Mohler & Wurtz, 1972, it was suggested that the intermediate layers have the biggest impacts downstream of the SC. This is also consistent with electrical microstimulation current thresholds for evoking saccades from the SC. 

We have addressed the reviewers’ comments about the intermediate layers having the biggest impact downstream of the SC in Public Reviews, Reviewer 3, Point 1. Furthermore, line 73 has been changed in the revised manuscript so that it now reads:

“As is the case for neurons in the superficial and intermediate layers, they [SC motor neurons] form a topographically organized map of visual space (White et al. 2017; Robinson 1972; Katnani and Gandhi 2011)”.  

(8) Line 100: there is an analogous literature regarding the question of why unwanted muscle contractions do not happen. Specifically, in the context of why SC visual bursts do not automatically cause saccades (which is a similar problem to the ones you mention about cognitive signals interfering by generating unwanted eye movements), both Jagadisan & Gandhi, Curr Bio, 2022 and Baumann et al, PNAS, 2023 also showed that SC population activity not only has different temporal structure (Jagadisan & Gandhi) but also occupy different subspaces (Baumann et al) under these two different conditions (visual burst versus saccade burst). This is conceptually similar to the idea that you are mentioning here with respect to arousal. So, it is worth it to mention these studies here and again in the discussion. 

We are grateful to the reviewer for these suggestions and have included text in the Introduction (Lines 125-128) and Discussion (Lines 678-682) of the revised manuscript along with the references cited above.

(9) Line 147: as mentioned above, it is now generally accepted that there are quite a few "pure" motor neurons in the SC. This is consistent with what you find. E.g. Baumann et al., 2023. And, again see Mohler and Wurtz in the 1970's. So, I wonder how useful it is to go too much into this idea of the deeper motor neurons (e.g. the correlations in the other panels of the Figure 1 supplement). 

This is related to the reviewer’s comment that the output of the SC might be in the intermediate layers. This concern has been addressed in Public Reviews, Reviewer 3, Point 1.

(10) Figure 1 should say where the RF was for the shown spike rasters. i.e. were these the same saccade target across trials? And where was that location relative to the RF? It would help also in the text to say whether the saccade was always to the RF center or whether you were randomizing the target location. 

We centered the array of saccade targets using the microstimulation-evoked eye movement for SC (see Methods section “Memory-guided saccade task”) to find the evoked eccentricity, and then used saccade targets with equal spacing of 45 degrees starting at zero (rightward saccade target). We did not do extensive RF mapping beyond this microstimulation centering. In Figure 1, the spike rasters are shown for a target that was visually identified to be within the neuron’s RF based on assessing responses to all 8 target angles. We have added information about this to the figure caption.

(11) Line 218: but were there changes in the eye movement statistics? For example, the slow drift eye movements during fixation? Or even the microsaccades? 

Addressed in Public Reviews, Reviewer 2, Point 2.  

(12) Line 248: shuffling what exactly? I think that more explanation would be needed here. 

Addressed in Public Reviews, Reviewer 1, Point 3.  

(13) Line 263: but isn't this reflecting a sensory transient in the pupil diameter, since the target just disappeared? 

Addressed in Public Reviews, Reviewer 3, Point 2.  

(14) Line 271: I suspect that slow drift eye movements (in between microsaccades) would show higher correlations. Not sure how well you can analyze those with a video-based eye tracker. 

We agree that fixational drift would be a worthwhile metric, but it is not one we have focused on here and to our knowledge does require higher precision tracking. 

(15) Line 286: again, see above about similar demonstrations with respect to the visual and motor burst intervals, which clearly cause the same problem (even stronger) as the one studied here. 

See reply, including Figure 2.

(16) Line 330: again, I'm not sure deeper necessarily automatically means closer to the output. For example, current thresholds for evoked saccades grow higher as you go deeper. Maybe the authors can ask their colleague Neeraj Gandhi about this point specifically, just to be safe. Maybe the safest would be to remain descriptive about the data, and just say something like: arousal-related fluctuations were absent in our deepest recorded sites. 

Addressed in Public Reviews, Reviewer 3, Point 1.

(17) Line 332: likewise, statements like this one here would be qualified if the output was the intermediate layers......anyway if I understand what I read so far in the paper, the signal will be anyway orthogonal to the motor burst population subspace. So, maybe there's no need to emphasize that it goes away in the very deepest layers. 

See reply above, Public Reviews, Reviewer 1, Point 4.

(18) Figure 3A: related to the above, I think one issue could be that the deeper contacts might already be out of the SC. Maybe some cell count distribution from each channel should help in this regard. i.e. were you finding way fewer saccade-related neurons in the deepest channels (even though the few that you found were with high motor index)? If so, then wouldn't this just mean that the channel was too deep? I think there needs to be an analysis like this, to convince readers that the channels were still in the SC. Ideally, electrical stimulation current thresholds for evoking saccades at different depths would be tested, but I understand that this can be difficult at this stage. 

Addressed in Public Reviews, Reviewer 3, Point 1.

(19) I keep repeating this because in general, cognitive effects are stronger in the intermediate/deeper layers than in the superficial layers. If these interfere with eye movements like arousal, then why should arousal be different?

Few studies have investigated the effects of attention on “pure” movement SC neurons that only discharge during a saccade. One study, which we cited in Introduction (Ignashchenkova et al., 2004, Nat. Neurosci.), found significant differences in spiking responses between trials with and without attentional cueing for visual and visuomotor neurons. No significant difference was found for motor neurons, consistent with our hypothesis that signals related to cognition and arousal are kept separate from saccade-related signals in the SC.

(20) The problem with Figure 5 and its related text is that the neurons with low motor index are additionally visual. So, of course, they can be modulated if the pupil diameter changes!

Addressed in Public Reviews, Reviewer 3, Point 2.  

(21) I had a hard time understanding Figure 6. 

See reply above, Public Reviews, Reviewer 1, Point 4.

(22) Line 586: these cells have more visual responses and will be affected by the amount of light entering the eye. 

Addressed in Public Reviews, Reviewer 3, Point 2.

I completely agree with this sentence I think establishing boundaries for your research is especially important but starting off with what your teacher has is important. For the context of academic papers written as a student your audience is a bit ambiguous generally speaking the only people who will read your academic papers is your professor and so understanding the guidelines and what necessarily the professor needs out of that paper is important. The purpose of the paper is to demonstrate that you not only can do research but that you are actively learning engaging and articulating the information you are researching. It's important that not only instructor headlines are clear and concise but also that in the moments that they aren't that we are asking and refining to ensure that it is an acceptable essay for the assignment.

The making of a personal index is a first step in building a mesh of knowledge. In just a few years, Vannevar Bush will speak of "associative trails" a phrase he uses twice in "As We May Think" (The Atlantic, July 1945), but of potentially more import is his phrase "associative indexing" which lays way to either juxtaposing or linking two ideas (either similar or disjoint) together. It bears asking the question of of whether it's more valuable to index and juxtapose similar ideas or disjoint ideas which may more frequently lead to better, more useful, and more relevant and rich future ideas.

It affords an immediate step, however, to associative indexing, the basic idea of which is a provision whereby any item may be caused at will to select immediately and automatically another. This is the essential feature of the memex. The process of tying two items together is the important thing. Bush, Vannevar. 1945. “As We May Think.” The Atlantic 176: 101–8. https://www.theatlantic.com/magazine/archive/1945/07/as-we-may-think/303881/ (October 22, 2022). #

See also the precursor of personal indexing which Mortimer J. Adler mentions in 1940: https://hypothes.is/a/cPcoAqhVEfC0rJOZ0Pm-8Q

Reviewer #3 (Public review):

Summary

The authors set out to explore the potential relationship between adult neurogenesis of inhibitory granule cells in the olfactory bulb and cumulative changes over days in odor-evoked spiking activity (representational drift) in the olfactory stream. They developed a richly detailed spiking neuronal network model based on Izhikevich (2003), allowing them to capture the diversity of spiking behaviors of multiple neuron types within the olfactory system. This model recapitulates the circuit organization of both the main olfactory bulb (MOB) and the piriform cortex (PCx), including connections between the two (both feedforward and corticofugal). Adult neurogenesis was captured by shuffling the weights of the model's granule cells, preserving the distribution of synaptic weights. Shuffling of granule cell connectivity resulted in cumulative changes in stimulus-evoked spiking of the model's M/T cells. Individual M/T cell tuning changed with time, and ensemble correlations dropped sharply over the temporal interval examined (long enough that almost all granule cells in the model had shuffled their weights). Interestingly, these changes in responsiveness did not disrupt low-dimensional stability of olfactory representations: when projected into a low-dimensional subspace, population vector correlations in this subspace remained elevated across the temporal interval examined. Importantly, in the model's downstream piriform layer, this was not the case. There, shuffled GC connectivity in the bulb resulted in a complete shift in piriform odor coding, including for low-dimensional projections. This is in contrast to what the model exhibited in the M/T input layer. Interestingly, these changes in PCx extended to the geometrical structure of the odor representations themselves. Finally, the authors examined the effect of experience on representational drift. Using an STDP rule, they allowed the inputs to and outputs from adult-born granule cells to change during repeated presentations of the same odor. This stabilized stimulus-evoked activity in the model's piriform layer.

Strengths

This paper suggests a link between adult neurogenesis in the olfactory bulb and representational drift in the piriform cortex. Using an elegant spiking network that faithfully recapitulates the basic physiological properties of the olfactory stream, the authors tackle a question of longstanding interest in a creative and interesting manner. As a purely theoretical study of drift, this paper presents important insights: synaptic turnover of recurrent inhibitory input can destabilize stimulus-evoked activity, but only to a degree, as representations in the bulb (the model's recurrent input layer) retain their basic geometrical form. However, this destabilized input results in profound drift in the model's second (piriform) layer, where both the tuning of individual neurons and the layer's overall functional geometry are restructured. This is a useful and important idea in the drift field, and to my knowledge, it is novel. The bulb is not the only setting where inhibitory synapses exhibit turnover (whether through neurogenesis or synaptic dynamics), and so this exploration of the consequences of such plasticity on drift is valuable. The authors also elegantly explore a potential mechanism to stabilize representations through experience, using an STDP rule specific to the inhibitory neurons in the input layer. This has an interesting parallel with other recent theoretical work on drift in the piriform (Morales et al., 2025 PNAS), in which STDP in the piriform layer was also shown to stabilize stimulus representations there. It is fascinating to see that this same rule also stabilizes piriform representations when implemented in the bulb's granule cells.

The authors also provide a thoughtful discussion regarding the differential roles of mitral and tufted cells in drift in piriform and AON and the potential roles of neurogenesis in archicortex.

In general, this paper puts an important and much-needed spotlight on the role of neurogenesis and inhibitory plasticity in drift. In this light, it is a valuable and exciting contribution to the drift conversation.

Weaknesses

I have one major, general concern that I think must be addressed to permit proper interpretation of the results.

I worry that the authors' model may confuse thinking on drift in the olfactory system, because of differences in the behavior of their model from known features of the olfactory bulb. In their model, the tuning of individual bulbar neurons drifts over time. This is inconsistent with the experimental literature on the stability of odor-evoked activity in the olfactory bulb.

In a foundational paper, Bhalla & Bower (1997) recorded from mitral and tufted cells in the olfactory bulb of freely moving rats and measured the odor tuning of well-isolated single units across a five-day interval. They found that the tuning of a single cell was quite variable within a day, across trials, but that this variability did not increase with time. Indeed, their measure of response similarity was equivalent within and across days. In what now reads as a prescient anticipation of the drift phenomenon, Bhalla and Bower concluded: "it is clear, at least over five days, that the cell is bounded in how it can respond. If this were not the case, we would expect a continual increase in relative response variability over multiple days (the equivalent of response drift). Instead, the degree of variability in the responses of single cells is stable over the length of time we have recorded." Thus, even at the level of single cells, this early paper argues that the bulb is stable.

This basic result has since been replicated by several groups. Kato et al. (2012) used chronic two-photon calcium imaging of mitral cells in awake, head-fixed mice and likewise found that, while odor responses could be modulated by recent experience (odor exposure leading to transient adaptation), the underlying tuning of individual cells remained stable. While experience altered mitral cell odor responses, those responses recovered to their original form at the level of the single neuron, maintaining tuning over extended periods (two months). More recently, the Mizrahi lab (Shani-Narkiss et al., 2023) extended chronic imaging to six months, reporting that single-cell odor tuning curves remained highly similar over this period. These studies reinforce Bhalla and Bower's original conclusion: despite trial-to-trial variability, olfactory bulb neurons maintain stable odor tuning across extended timescales, with plasticity emerging primarily in response to experience. (The Yamada et al., 2017 paper, which the authors here cite, is not an appropriate comparison. In Yamada, mice were exposed daily to odor. Therefore, the changes observed in Yamada are a function of odor experience, not of time alone. Yamada does not include data in which the tuning of bulb neurons is measured in the absence of intervening experience.)

Therefore, a model that relies on instability in the tuning of bulbar neurons risks giving the incorrect impression that the bulb drifts over time. This difference should be explicitly addressed by the authors to avoid any potential confusion. Perhaps the best course of action would be to fit their model to Mizrahi's data, should this data be available, and see if, when constrained by empirical observation, the model still produces drift in piriform. If so, this would dramatically strengthen the paper. If this is not feasible, then I suggest being very explicit about this difference between the behavior of the model and what has been shown empirically. I appreciate that in the data there is modest drift (e.g., Shani-Narkiss' Figure 8C), but the changes reported there really are modest compared to what is exhibited by the model. A compromise would be to simply apply these metrics to the model and match the model's similarity to the Shani-Narkiss data. Then the authors could ask what effect this has on drift in piriform.

The risk here is that people will conclude from this paper that drift in piriform may simply be inherited from instability in the bulb. This view is inconsistent with what has been documented empirically, and so great care is warranted to avoid conveying that impression to the community.

Major comments (all related to the above point)

(1) Lines 146-168: The authors find in their model that "individual M/T cells changed their responses to the same odor across days due to adult-neurogenesis, with some cells decreasing the firing rate responses (Fig.2A1 top) while other cells increased the magnitude of their responses (Fig. 2A2 bottom, Fig. S2)" they also report a significant decrease in the "full ensemble correlation" in their model over time. They claim that these changes in individual cell tuning are "similar to what has been observed by others using calcium imaging of M/T cell activity (Kato et al., 2012 and Yamada et al., 2017)" and that the decrease in full ensemble correlation is "consistent with experimental observations (Yamada et al., 2017)." However, the conditions of the Kato and Yamada experiments that demonstrate response change are not comparable here, as odors were presented daily to the animals in these experiments. Therefore, the changes in odor tuning found in the Kato and Yamada papers (Kato Figure 4D; Yamada Figure 3E) are a function of accumulated experience with odor. This distinction is crucial because experience-induced changes reflect an underlying learning process, whereas changes that simply accumulate over time are more consistent with drift. The conditions of their model are more similar to those employed in other experiments described in Kato et al. 2012 (Figure 6C) as well as Shani-Narkiss et al. (2023), in which bulb tuning is measured not as a function of intervening experience, but rather as a function of time (Kato's "recovery" experiment). What is found in Kato is that even across two months, the tuning of individual mitral cells is stable. What alters tuning is experience with odor, the core finding of both the Kato et al., 2012 paper and also Yamada et al., 2017. It is crucial that this is clarified in the text.