Reviewer #1 (Public Review):

Zhang et al. tackle the important topic of primate-specific structural features of the brain and the link with functional specialization. The authors explore and compare gyral peaks of the human and macaque cortex through non-invasive neuroimagery, using convincing techniques that have been previously validated elsewhere. They show that nearly 60% of the macaque peaks are shared with humans, and use a multi-modal parcellation scheme to describe the spatial distribution of shared and unique gyral peaks in both species.

The claim is made that shared peaks are mainly located in lower-order cortical areas whereas unique peaks are located in higher-order regions, however, no systematic comparison is made. The authors then show that shared peaks are more consistently found across individuals than unique peaks, and show a positive but small and non-significant correlation between cross-individual counts of the shared peaks of the human and the macaque i.e. the authors show a non-significant trend for shared peaks that are more consistently found across humans to be those that are also more found across macaques.

In order to identify if unique and shared peaks could be identified based on the structural features of the cortical regions containing them, the authors compared them with t-tests. A correction for multiple comparisons should be applied and t-values reported. Graph-theoretical measures were applied to functional connectivity datasets (resting-state fMRI) and compared between unique and shared peak regions for each species separately. Again the absence of multiple comparison correction and t-values make the results hard to interpret. The same comment applies to the analysis reporting that shared peaks are surrounded by a larger number of brain regions than unique peaks. Finally, the potentially extremely interesting results about differential human gene expression of shared and unique peaks regions are not systematically reported e.g. the 28 genes identified are not listed and the selection procedure of 7 genes is not fully reported.

The paper is well written and the methods used for data processing are very compelling i.e. the peak cluster extraction pipeline and cross-species registration.

Comments on revision:

The authors have convincingly addressed all my previous concerns such that, as the revised paper stands now, the presented results provide solid support for the conclusions of the authors. The revised paper is now of interest for a large part of the neuroscience community and specifically for those interested in primate-specific structural features of the brain and the link with functional specialization.

eLife assessment

This study by Ghafari et al. tackles a question relevant for the field of attention as it connects structural differences in subcortical regions with oscillatory modulations during attention allocation. Using a combination of Magnetoencephalography (MEG) and magnetic resonance imaging (MRI) data in human subjects, the valuable results show that inter-individual differences in the lateralisation of alpha oscillations are explained by asymmetry of subcortical brain regions. The strength of evidence is deemed convincing in line with current state-of-the-art.

Reviewer #1 (Public Review):

Summary:

The authors re-analysed the data of a previous study in order to investigate the relation between asymmetries of subcortical brain structures and the hemispheric lateralization of alpha oscillations during visual spatial attention. The visual spatial attention task crossed the factors of target load and distractor salience, which made it possible to also test the specificity of the relation of subcortical asymmetries to lateralized alpha oscillations for specific attentional load conditions. Asymmetry of globus pallidus, caudate nucleus, and thalamus explained inter-individual differences in attentional alpha modulation in the left versus right hemisphere. Multivariate regression analysis revealed that the explanatory potential of these regions' asymmetries varies as a function of target load and distractor salience.

In the revision of the article, the authors addressed my concerns.

However, my concern with regard to the statistical analysis of the specificity of certain subcortical regions predicting HLM seems to be not fully addressed. The authors added an additional statistical analysis for "testing the null hypothesis that a given regressor does not impact all dependent variables". To my understanding, this is a somewhat unusual definition of a null hypothesis. Typically, the null hypothesis is the hypothesis of no effect, meaning here it should state that the effect is the same across predictors.

In the new statistical analysis, the authors seem to take non-significant results (p>.05) as evidence for the specificity of subcortical regions in predicting HLM. The rationale of this statistical approach is difficult to follow and was somewhat unclear to me.

A much simpler and more straight-forward approach would be to contrast beta-estimates per subcortical region between experimental conditions. For instance, if the beta estimates in the thalamus for the "low-load target, non-salient distractor" condition would be significantly larger than the beta estimates for the other conditions, this would speak to specificity.

eLife assessment

Parkkinen et al. describe distinct biophysical profiles of brain-derived alpha-synuclein vs. in vitro-seeded synuclein fibrils. The findings are important and relevant to the emerging potential role of SAA as a biomarker of PD. The evidence is solid, using appropriate methodology and providing some support for the main claims with some limitations.

Reviewer #1 (Public Review):

SUMMARY:

Parkinson's disease (PD) and other synucleinopathies, including Parkinson's Disease Dementia (PDD), Dementia with Lewy Bodies (DLB), and Multiple System Atrophy (MSA), pose significant challenges for early diagnosis, as their clinical manifestations often emerge after substantial neurodegeneration has occurred. In this context, the Alpha-Synuclein Seeding Amplification Assay (SAA) has garnered considerable attention for its potential as a diagnostic tool, capable of detecting pathological forms of alpha-synuclein (αSyn) even before the onset of classical clinical symptoms and signs. The assay exploits αSyn's intrinsic property to convert healthy forms into pathological ones, subsequently amplifying these pathological forms for visualization. This study aims to investigate the efficacy of SAA in accurately identifying subtypes of synucleinopathies, including PD, PDD, DLB, and MSA. To achieve this, the results from the patient brain-derived αSyn SAA are compared with those obtained through conformational stability assays, immunolabeling, and electron microscopy. Study shows that brain-derived αSyn fibrils exhibit significant differences across various synucleinopathies in their conformation, biochemical profile and phosphorylation patterns. Importantly, the SAA method appears to fall short in capturing these distinctions.

The study's findings are highly relevant given the rapidly advancing landscape of utilizing the SAA for the diagnosis and differentiation of various forms of PD and synucleinopathies using patient biofluids. It is somewhat surprising that the authors primarily characterize SAA as a research tool without delving into its potential as a biomarker detection assay, especially in the context of the field's excitement about its diagnostic applications. Additionally, a missed opportunity lies in not referencing a recent study that employed SAA successfully to diagnose PD and subtype the condition using a vast sample size. To further strengthen the results, the inclusion of healthy control brains in the biochemical and immunostaining/immunoblot experiments would provide more robust comparisons. Overall, the authors have conducted their experiments diligently, and their study offers valuable insights that align with the ongoing efforts to enhance early diagnosis and subtype differentiation in the domain of synucleinopathies.

STRENGTH:

The strengths of this research article are indeed notable and contribute to the credibility and significance of the study:

Important Research Question: The study addresses a crucial question in the field of neurodegenerative diseases by evaluating the effectiveness of the αSyn SAA in diagnosing and differentiating synucleinopathies. This question is of significant clinical and scientific interest.<br /> Comprehensive Introduction: The article provides a thorough and well-structured introduction to the topic with an illustration, setting the stage for the research. It ensures that readers, including those unfamiliar with the subject matter, can grasp the context and significance of the study.<br /> Use of Patient Brain Tissue: The use of patient-derived brain tissue samples from various synucleinopathies, including PD, PDD, DLB, and MSA, enhances the clinical relevance and applicability of the findings.<br /> Replication and Statistical Significance: Conducting the experiments six times for each sample demonstrates the rigor of the study and the robustness of the results, and increases the confidence in the conclusions drawn.<br /> Clarity in Experimental Results and Discussion: The authors have presented the experimental results in a clear and understandable manner. I was personally impressed by images showing twisted and straight conformations of αSyn, as well as immunogold labeling for phosphorylation of αSyn, which aids in conveying the findings effectively to the readers. The results clearly show distinct differences in the characteristics of αSyn fibrils across different synucleinopathies. It also highlights the more aggressive seeding capacities and higher biochemical stability of αSyn in PDD and DLB patients, offering valuable insights into the pathophysiology of these conditions. The authors also clearly show that SAA fails in differentiating the disease types within the synucleinopathies.<br /> Clinical relevance: The study underscores the importance of considering complementary diagnostic methods alongside SAA for a more comprehensive understanding of synucleinopathy subtypes. The study might also play an important role in potential FDA approval of SAA as a diagnostic tool for synucleinopathies, especially for PD.<br /> These strengths collectively make the study a valuable contribution to the field of neurodegenerative diseases, shedding light on the limitations and potential applications of SAA in the diagnosis and differentiation of various synucleinopathies.

WEAKNESS:

While this study is overall robust, there are several aspects that could further enhance the quality and interpretation of the findings.

Clinical Data on Patient Brain Samples: The inclusion of specific details such as post-mortem intervals and the age at disease onset for patient brain samples would be valuable. These factors could significantly affect the quality of the tissues and their relevance to the study. Moreover, given the large variation in disease duration between PD and PDD, it's important to consider disease duration as a potential confounding factor, especially when concluding that PDD patients have a more severe form of synucleinopathy compared to PD.<br /> Inclusion of Healthy Controls in Multiple Tests: Given the importance of healthy controls in scientific studies, especially those involving human brain samples, the authors could consider using healthy controls in more tests to strengthen the robustness of the findings. Expanding the use of healthy controls in biochemical profiling and phosphorylation profiles would provide a better basis for comparison and clarify the significance of results in a disease context.<br /> This will help the authors to elaborate on the interpretation of results, for example, in Figure 3, where the authors claim that PD brains show mostly monomeric αSyn forms (line 119 and 120, and also in 222 and 223). Whether it implies the absence of alpha-syn pathology in PD brains? If there are differences from healthy controls? What are these low molecular weight bands (<15kD) (line 125-126) and whether they are also present in healthy controls? Also, we do not have a perfect pS129-specific (anti-p𝛼Syn) antibody. They are known for non-specific labeling. Investigating the phosphorylation levels in healthy controls and comparing them to PD brains, especially considering the predominance of monomeric (healthy αSyn?) in PD brains, would help clarify the observed changes.<br /> Age of Healthy Controls: Providing information about the age at death for healthy controls is crucial, as age can impact the accumulation of αSyn. Also include if the brain samples were age-matched, or analyses were age-adjusted.<br /> Braak Staging Discrepancy: The study reports the same Braak staging for both PD and PDD, despite the significant difference in disease duration. Maybe other reviewers with clinical experience might have a better take on this. This observation merits discussion in the paper, allowing readers to better understand the implications of this finding.<br /> Citation of Relevant Studies: The paper should consider citing and discussing a recent celebrated study on PD biomarkers that used thousands of cerebrospinal fluid (CSF) samples from different PD patient cohorts to demonstrate the effectiveness of SAA as a biochemical assay for diagnosing PD and its subtypes (https://doi.org/10.1016/S1474-4422(23)00109-6).<br /> In summary, these suggestions aim to enhance the study's quality and the clarity of its findings, ultimately contributing to a more comprehensive understanding of synucleinopathies and the diagnostic potential of SAA.

Reviewer #2 (Public Review):

Most neurodegenerative diseases are characterized by the self-templated misfolding of a particular protein in a manner that enables progressive spread throughout the central nervous system. In diseases including Parkinson's disease (PD) and multiple system atrophy (MSA), the protein alpha-synuclein misfolds into unique shapes, or strains, which use this self-replicating mechanism to encode disease-specific information. Previous research suggests that a major contributor to the lack of successful clinical trials across neurodegenerative diseases is the lack of disease-relevant strains used in preclinical testing. While MSA patient samples are known to replicate efficiently in cell and mouse models of disease, Lewy body disease (LBD) patient samples do not. To overcome this obstacle, the seeding amplification assay (SAA) uses recombinant alpha-synuclein to amplify the misfolded protein structure present in a human patient sample. The resulting fibrils are then widely used by many laboratories as a model of PD. In this manuscript, Lee et al., set out to compare the strain properties of alpha-synuclein fibrils isolated from LBD and MSA patient samples with the resulting amplified fibrils following SAA. Using orthogonal biochemical and structural approaches to strengthen their analyses, the authors report that the SAA-amplified fibrils do not recapitulate the disease-relevant strains present in the patient samples. Moreover, their data suggest that regardless of which strain is used to seed the SAA reaction, the same strain is generated. These results clearly demonstrate that the SAA-amplified material is not disease-relevant. SAA fibrils are broadly used in academic and pharmaceutical laboratories. They are used in ongoing drug discovery efforts and recombinant fibrils broadly inform much of what is known about alpha-synuclein strain biology in LBD patients. The implications of the reported work are, therefore, expansive. These findings add to the growing ledger of reasons that the use of SAA fibrils in research should be halted until improved methods for amplification with high fidelity are developed.

Reviewer #3 (Public Review):

Summary:

This interesting manuscript presents a comparison of biophysical properties, TEM appearances, and phosphorylation patterns of brain-derived synuclein fibrils from 3 subjects each with Parkinson Disease (PD), Parkinson Disease with Dementia (PDD), Dementia with Lewy bodies (DLB) and Multiple System Atrophy (MSA), the effects of studying these brain-derived fibrils in a Seeding Aggregation Assay (SAA), and a comparison of the seeded and resultant fibers. The results are not unexpected.

Strengths:

The work explores an important question. Namely, what is the fidelity of synuclein fibrils produced during an SAA reaction to the starting material if that material has been extracted from the brains of deceased patients with synucleinopathies.

Weaknesses:

The work suffers from several methodological flaws

The experiments are missing two important controls. 1) what to fibrils generated by different in vitro fibril preparations made from recombinant synclein protein look like; and 2) the use of CSF from the same patients whose brain tissue was used to assess whether CSF and brain seeds look and behave identically. The latter is perhaps the most important question of all - namely how representative are CSF seeds of what is going on in patients' brains?

In their discussion the authors do not comment on the obvious differences in the conditions leading to the formation of seeds in the brain and in the artificial conditions of the seeding assay. Why should the two sets of conditions be expected to yield similar morphologies, especially since the extracted fibrils are subjected to harsh conditions for solubilization and re-suspension.

Finally, the key experiment was not performed - would the resultant seeds from SAA preparations from the different nosological entities produce different pathologies when injected into animal brains? But perhaps this is the subject of a future manuscript.

Furthermore, the authors comment on phosphorylation patterns, stating that the resultant seeds are less heavy phosphorylated than the original material. Again, this should not be surprising, since the SAA assay conditions are not known to contain the enzymes necessary to phosphorylate synuclein. The discussion of PTMs is limited to pS-129 phosphorylation. What about other PTMs? How does the pattern of PTMs affect the seeding pattern.

Lastly, the manuscript contains no data on how the diagnostic categories were assigned at autopsy. This information should be included in the supplementary material.

eLife assessment

Songbirds provide a tractable model system to study mechanisms of vocal production and sequencing, and past work showed that the lesions to LMAN, the output of a basal ganglia thalamocortical loop, reduced vocal variability, consistent with a role in motor exploration. In this fundamental work, the authors rigorously examined how lesions to an understudied neighboring region, MMAN, part of a parallel basal ganglia loop, affect singing in Bengalese finches, whose songs exhibit complex sequential transitions. The authors provide compelling evidence that MMAN lesions resulted in increased sequential variability but do not affect syllable acoustic structure, showing that distinct frontal systems can have distinct functions for producing and sequencing song syllables.

Reviewer #1 (Public Review):

Summary:

Songbirds provide a tractable system to examine neural mechanisms of sequence generation and variability. In past work, the projection from LMAN to RA (output of the anterior forebrain pathway) was shown to be critical for driving vocal variability during babbling, learning, and adulthood. LMAN is immediately adjacent to MMAN, which projects to HVC. MMAN is less well understood but, anatomically, appears to resemble LMAN in that it is the cortical output of a BG-thalamocortical loop. Because it projects to HVC, a major sequence generator for both syllable phonology and sequence, a strong prediction would be that MMAN drives sequence variability in the same way that LMAN drives phonological variability. This hypothesis predicts that MMAN lesions in a Bengalese finch would reduce sequence variability. Here, the authors test this hypothesis. They provide a surprising and important result that is well motivated and well analyzed: MMAN lesions increase sequence variability - this is exactly the opposite result from what would be predicted based on the functions of LMAN.

Strengths:

(1) A very important and surprising result shows that lesions of a frontal projection from MMAN to HVC, a sequence generator for birdsong, increase syntactical variability.

(2) The choice of Bengalese finches, which have complex transition structures, to examine the mechanisms of sequence generation, enabled this important discovery.

(3) The idea that frontal outputs of BG-cortical loops can generate vocal variability comes from lesions/inactivations of a parallel pathway from LMAN to RA. The difference between MMAN and LMAN functions is striking and important.

eLife assessment

These ingenious and thoughtful studies present important findings concerning how people can represent and generalise abstract patterns of sensory data. The issue of generalization is a core topic in neuroscience and psychology, relevant across a wide range of areas, and the findings will be of interest to researchers across areas in perception, learning and cognitive science. The findings are convincing in this setting, but future research must establish their generality and interrogate the precise nature of the underlying mechanism.

Reviewer #1 (Public Review):

Summary:

This manuscript reports a series of experiments examining category learning and subsequent generalization of stimulus representations across spatial and nonspatial domains. In Experiment 1, participants were first trained to make category judgments about sequences of stimuli presented either in nonspatial auditory or visual modalities (with feature values drawn from a two-dimensional feature manifold, e.g., pitch vs timbre), or in a spatial modality (with feature values defined by positions in physical space, e.g., Cartesian x and y coordinates). A subsequent test phase assessed category judgments for 'rotated' exemplars of these stimuli: i.e., versions in which the transition vectors are rotated in the same feature space used during training (near transfer) or in a different feature space belonging to the same domain (far transfer). Findings demonstrate clearly that representations developed for the spatial domain allow for representational generalization, whereas this pattern is not observed for the nonspatial domains that are tested. Subsequent experiments demonstrate that if participants are first pre-trained to map nonspatial auditory/visual features to spatial locations, then rotational generalization is facilitated even for these nonspatial domains. It is argued that these findings are consistent with the idea that spatial representations form a generalized substrate for cognition: that space can act as a scaffold for learning abstract nonspatial concepts.

Strengths:

I enjoyed reading this manuscript, which is extremely well written and well presented. The writing is clear and concise throughout, and the figures do a great job of highlighting the key concepts. The issue of generalization is a core topic in neuroscience and psychology, relevant across a wide range of areas, and the findings will be of interest to researchers across areas in perception and cognitive science. It's also excellent to see that the hypotheses, methods and analyses were pre-registered.

The experiments that have been run are ingenious and thoughtful; I particularly liked the use of stimulus structures that allow for disentangling of one-dimensional and two-dimensional response patterns. The studies are also well powered for detecting effects of interest. The model-based statistical analyses are thorough and appropriate throughout (and it's good to see model recovery analysis too). The findings themselves are clear-cut: I have little doubt about the robustness and replicability of these data.

Weaknesses:

In my original review I raised a concern related to a potential alternative interpretation of the findings: the idea that participants have substantial experience of representing space in terms of multiple, independent, and separable dimensions, whereas this may not be the case for the visual and auditory stimuli used here. As I noted in that prior review, on this view "the impact of spatial pre-training and (particularly) mapping is simply to highlight to participants that the auditory / visual stimuli comprise two separable (and independent) dimensions."

In addressing this point, the authors note that performance in the visual/auditory "mapping" task in Experiments 2c and 3c suggests that most participants were paying attention to both dimensions of auditory and visual stimuli. I agree that seems to have been the case. But there is a difference between making use of information from both dimensions, and realizing that ***the two dimensions are separable and independent*** (which is what is required for rotational generalization in this task).

As an analogy, suppose I have a task where participants have to map a pillow and a shuttlecock to category A, and a surfboard and a bicycle to category B. A participant could learn to do this just by memorizing the correct response for each item considered as a "whole thing". Or they could realize that the items contain component information, learning that "things with feathers" belong in category A, and "things that can carry people" go in category B. Performance may be the same in both cases, but the underlying process is quite different.

The "attention to dimensions" account that I advanced in my previous review was referring to something more like the latter (feathers/vehicle) case: that spatial pre-training helps people to understand that items can be decomposed into separable pieces of information. Above-chance performance in the visual-auditory mapping task does not (necessarily) demonstrate this ability because it could reflect memorization of "whole" stimuli rather than reflecting decomposition into separable component parts. I agree that it does at least show that participants were paying attention to and making use of information from both dimensions when making their mapping decisions; it's just that they may not have *realized* that they were using information from two separable dimensions.

eLife assessment

The authors provide convincing experimental evidence of extended motivational signals encoded in the mouse anterior cingulate cortex (ACC) that are implemented by the orbitofrontal cortex (OFC)-to-ACC signaling during learning. The results are valuable to the field of motivation and cognition. The experimental methods used were state-of-the-art. The manuscript would further benefit from theory-driven analyses to inform a mechanistic understanding, particularly for the single-cell calcium imaging results. These results will be of interest to those interested in cortical function, learning, and/or motivation.

Reviewer #1 (Public Review):

Summary:

This is an interesting report examining activity patterns in mouse ACC and in the OFC neurons projecting to ACC. In addition, the effects of inactivation are examined. In aggregate, the results provide new and interesting information about these two brain areas and they translate motivation into action - a function that it seems intuitively plausible that ACC might perform but, despite this intuition, there have been comparatively few direct tests of the idea and little is known of the specific mechanisms. The study is performed carefully and is written up clearly. There were just a few points where I wondered if a little more clarification might be helpful.

Strengths:

The combination of recording and inactivation/inhibition experiments and the combination of investigation of ACC neurons and of OFC regions projecting to ACC are very impressive.

Weaknesses:

These are all minor points of clarification.

(1) An important conclusion (Figure 4) is that when mice are trained to run through no reward (N) cues in order to reach reward (R) cues, the OFC neurons projecting to ACC each respond to different specific events in a manner that ensures that collectively they tile the extended behavioural sequence. What I was less sure of was whether the ACC neurons do the same or not. Figure 3 suggests that on average ACC neurons maintain activity across N cues in order to get to R cues but I was not sure whether this was because all individual neurons did this or whether some had activity patterns like the OFC neurons projecting to ACC.

(2) Figure 1 versus Figure 2: There does not seem to be a particular motivation for whether chemogenetic inactivation or optogenetic inhibition were used in different experiments. I think that this is not problematic but, if I am wrong and there were specific reasons for performing each experiment in a certain way, then further clarification as to why these decisions were made would be useful. If there is no particular reason, then simply explaining that this is the case might stop readers from seeking explanations.

(3) P5, paragraph 2. The authors argue that OFC and anteriomedial (AM) thalamic inputs into ACC are especially important for mediating motivation through N cues in order to reach R cues. Is this based on a statistical comparison between the activity in OFC or AM inputs as opposed to the other inputs?

(4) P3, paragraph 2. Some papers by Khalighinejad and colleagues (eg Neuron 2020, Current Biology, 2022) might be helpful here in as much as they assess ACC roles in determining action frequency, initiation, and speed and mediating the relationship between reward availability and action frequency and speed.

(5) Paragraph 1 "This learning is of a more deliberate, informed nature than habitual learning, as they are sensitive to the current value of outcomes and can lead to a novel sequence of actions for a desired outcome1-3." Should "they" be "it"?

Reviewer #2 (Public Review):

Summary:

Regalado et al. studied how an extended motivational state, necessary for maintaining behavioural drive despite unrewarding experiences, could be encoded in the ACC and its potential causal implications for learning discriminatory behaviour and avoiding unrewarding stimuli. They designed a self-initiated learning task and identified bulk neural responses tuned specifically to reward delivery as well as trial initiation. Interestingly, in both cases, neural activity precedes behavioural onset, indicating the encoding of a motivational signal. To investigate the neural encoding of motivational signals during unrewarded, distracting stimuli presentation, they created a discrimination task by introducing 'no reward' cues, during which animals need to learn not to reduce running speed and not engage in licking. Interestingly, with mice learning to increase running speed and reduce licking rates after 'no reward' cues, the preceding ACC activity also gradually increased. Importantly, only the increase in running speed after 'no reward' cues was impaired upon optogenetic inhibition of ACC activity during early training, linking the extended motivational signal in ACC and learning to maximise rewards by actively avoiding distracting and unrewarded stimuli. Such motivational signals could also be observed in OFC-ACC projecting neurons. Especially the continuous ramping of activity upon repeated 'non-reward' cues, which could be exclusively observed in the 'fast learner' subgroup, provides an interesting concept of how an extended motivational signal necessary for learning avoidance of unrewarded stimuli could be implemented in ACC. The shift in the temporal activity of initially reward-responsive neurons towards the preceding 'no reward' cue, provides a potential mechanism linking extended motivation to reward maximisation. This mechanism seems to be particularly important in periods of persistent 'non-reward' cues, as demonstrated in the impairment of running speed increase after two consecutive 'non-reward' cues.

Appraisal:

The authors provide convincing experimental evidence to support their claims of an extended motivational signal encoded in the ACC that is implemented by OFC-ACC signalling and critically involved in learning avoidance of unrewarded stimuli. The newly designed task seems appropriate to identify correlates of relevant cognitive and behavioural variables (e.g. sustained motivation). The combination of recording Ca2+ transients (bulk as well as longitudinal single neuron recordings) to identify potential neural responses and subsequent evaluation of their causal role in establishing and maintaining this persistent motivational state using opto- and pharmacogenetic manipulations is generally accepted.

Impact:

The findings will be valuable for further research on the impact of motivational states on behaviour and cognition. The authors provided a promising concept of how persistent motivational states could be maintained, as well as established a novel, reproducible task assay. While experimental methods used are currently state-of-the-art, theoretical analysis seems to be incomplete/not extensive.

eLife assessment

This study presents important methodologies for repeated brain ultrasound localization microscopy (ULM) in awake mice and a set of results indicating that wakefulness reduces vascularity and blood flow velocity. The efficiency of the technique is however incompletely demonstrated, in particular regarding the reliability of longitudinal imaging. This study is relevant for scientists investigating vascular physiology in the brain.

Reviewer #1 (Public Review):

Summary:

Wang and colleagues present a study aimed at demonstrating the feasibility of repeated ultrasound localization microscopy (ULM) recording sessions on mice chronically implanted with a cranial window transparent to ultrasound. They provided quantitative information on their protocol, such as the required number of contrast-enhancing microbubbles (MBs) to get a clear image of the vasculature of a brain coronal section. Also, they quantified the co-registration quality over time-distant sessions and the vasodilator effect of isoflurane.

Strengths:

The study showed a remarkable performance in recording precisely the same brain coronal section over repeated imaging sessions. In addition, it sheds light on the vasodilator effect of isoflurane (an anesthetic whose effects are not fully understood) on the different brain vasculature compartments, although, as the authors stated, some insights in this aspect have already been published with other imaging techniques. The experimental setting and protocol are very well described.

Weaknesses:

While the title is fair with respect to the data shown, in the summary and the rest of the paper, the comparison between anesthetized and awake conditions is systematically stated, while more caution should be used.

First, isoflurane is one of the (many) anesthetics commonly used in pre-clinical research, and its effect on the brain vasculature cannot be generalized to all the anesthetics. Indeed, other anesthesia approaches do not produce evident vasodilation; see ketamine + medetomidine mixtures. Second, the imaged awake state is head-fixed and body-constrained in mice. A condition that can generate substantial stress in the animals. In this study, there is no evaluation of the stress level of the mice. In addition, the awake imaging sessions were performed a few minutes after the mouse woke up from isoflurane induction, which is necessary to inject the MB bolus. It is known that the vasodilator effects of isoflurane last a long time after its withdrawal. This aspect would have influenced the results, eventually underestimating the difference with respect to the awake state.

These limitations should be clearly described in the Discussion.

Looking at Figure 2e, it takes more than 5' to reach the 5 Millions MB count useful for good imaging. However, the MB count per pixel drops to a few % at that time. This information tells me that (i) repeated measurements are feasible but with limited brain coverage since a single 'wake up' is needed to acquire a single brain section and (ii) this approach cannot fit the requirements of functional ULM that requires to merge the responses to multiple stimuli to get a complete functional image. Of course, a chronic i.v. catheter would fix the issue, but this configuration is not trivial to test in the experimental setup proposed by the authors, hindering the extension of the approach to fULM.

Statistics are often poor or not properly described. The legend and the text referring to Figure 2 do not report any indication of the number of animals analyzed. I assume it is only one, which makes the findings strongly dependent on the imaging quality of THAT mouse in THAT experiment. Three mice have been displayed in Figure 3, as reported in the text, but it is not clear whether it is a mouse for each shown brain section. Figure 5 reports quantitative data on blood vessels in awake VS isoflurane states but: no indication about the number of tested mice is provided, nor the number of measured blood vessels per type and if statistics have been done on mice or with a multivariate method. Also, a T-test is inappropriate when the goal is to compare different brain regions and blood vessel types. Similar issues partially apply to Figure 6, too.

Reviewer #2 (Public Review):

Summary:

The authors present a very interesting collection of methods and results using brain ultrasound localization microscopy (ULM) in awake mice. They emphasize the effect of the level of anesthesia on the quantifiable elements assessable with this technique (i.e. vessel diameter, flow speed, in veins and arteries, area perfused, in capillaries) and demonstrate the possibility of achieving longitudinal cerebrovascular assessment in one animal during several weeks with their protocol.

Strengths:

Even if the methods elements considered separately are not new (brain ULM in rodents, setup for longitudinal awake imaging similar to those used in fUS imaging, quantification of vessel diameters/bubble flow/vessel area), when masterfully combined as it is done in this paper, they answer two questions that have been long-running in the community: what is the impact of anesthesia on the parameters measured by ULM (and indirectly in fUS and other techniques)? Is it possible to achieve ULM in awake rodents for longitudinal imaging? The authors answer quite exhaustively the first question. The manuscript is well-constructed and well-written, and the graphics are appealing.

Weaknesses:

The only major comment (calling for further work) I would like to make is the relative weakness of the manuscript regarding longitudinal imaging (mostly Figure 6), compared to the exhaustive review of the effect of isoflurane on the vasculature (3 rats, 3 imaging planes, quantification on a large number of vessels, in 9 different brain regions). The 6 cortical vessels evaluated in Figure 6 feel really disappointing. As longitudinal imaging is supposed to be the salient element of this manuscript (first word appearing in the title), it should be as good and trustworthy as the first part of the paper. Figure 6c. is of major importance, and should be supported by a more extensive vessel analysis, including various brain areas, and validated on several animals to validate the robustness of longitudinal positioning with several instances of the surgical procedure. Figure 6d estimates the reliability of flow measurements on 3 vessels only. Therefore I recommend showing something similar to what is done in Figures 4 and 5: 3 animals, and more extensive quantification in different brain regions.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Wang et al. performed a study looking at vascular changes in response to anesthesia in awake mice using ultrasound localization microscopy (ULM). The authors report a reduction of vascularity and blood flow velocity in the awake state. In addition, they demonstrate the reproducibility of ULM measurements in time.

Strengths:

Demonstration that high-quality, state-of-the-art ULM images can be performed using cranial windows in awake animals.<br /> Demonstration that repeated imaging in time produces comparable images.

Weaknesses:

It is unclear whether multiple animals were used in the statistical analysis.<br /> Generalizations are sometimes drawn from what seems to be the analysis of a single vessel.<br /> The description of the statistical analysis is mostly qualitative.<br /> Some terms used are insufficiently defined.<br /> Additional limitations should be included in the discussion.<br /> Some technical details are lacking.

Without information about whether the results obtained come from multiple animals, it is difficult to conclude that the authors generally achieved their aim. They do achieve it in a single animal.

The results that are shown are interesting and could have an impact on the ULM community and beyond. In particular, the experimental setup they used along with the high reproducibility they report could become very important for the use of ULM in larger animal cohorts.

Reviewer #2 (Public Review):

The authors combine genetic tools, dye fills and connectome analysis techniques to generate a "first-of-its-kind", near complete, synaptic resolution map of the head bristle neurons of Drosophila. While some of the BMN anatomy was already known based on previous work by the authors and other researchers, this is the first time a near complete map has been created for the head BMNs at electron microscopy resolution.

Strengths:

(1) The authors cleverly use techniques that allow moving back and forth between periphery (head bristle location) and brain, as well as moving between light microscopy and electron microscopy data. This allows them to first characterize the pathways taken by different head BMNs to project to the brain and also characterize anatomical differences among individual neurons at the level of morphology and connectivity.<br /> (2) The work is very comprehensive and results in a near complete map of all head BMNs.<br /> (3) Authors also complement this anatomical characterization with a first-level functional analysis using optogenetic activation of BMNs that results in expected directed grooming behavior.

Weaknesses:<br /> (1) While not strictly needed here, it could help provide context if authors revealed some of the important downstream pathways that could explain optogenetics behavioral phenotypes: This point was addressed by authors in the revisions and I agree a detailed description of downstream circuits is not needed at this point.<br /> (2) In contrast to the rigorous quantitative analysis of the anatomical data, the behavioral data is analyzed using much more subjective methods. While I do not think it is necessary to perform a rigorous analysis of behaviors in this anatomy focused manuscript, the conclusions based on behavioral analysis should be treated as speculative in the current form e.g. calling "nodding + backward motions" as an avoidance response is not justified as it currently stands. Strong optogenetic activation could lead to sudden postural changes that due to purely biomechanical constraints could lead to a couple of backward steps as seen in the example videos. Moreover since the quantification is manual, it is not clear what the analyst interprets as backward walking or nodding. Interpretation is also concerning because controls show backward walking (although in fewer instances based on subjective quantification): This point was addressed by the authors during revisions and I'm mostly satisfied with their response, where authors agree that the behavioral results are currently used to speculate about the role of BMNs in aversive behaviors. Still, the fact that controls show some "backward motions" is a bit concerning when talking about "significant differences" between control and test groups based on manual annotations and I would recommend future studies focusing on these behaviors to use more unbiased quantitative analysis wherever possible.

Summary:

The authors end up generating a near-complete map of head BMNs that will serve as a long-standing resource to the Drosophila research community. This will directly shape future experiments aimed at modeling or functionally analyzing the head grooming circuit to understand how somatotopy guides behaviors. I appreciate the authors taking the time to revise the manuscript and address reviewer concerns.

Reviewer #3 (Public Review):

Eichler et al. set out to catalog the mechanosensory bristles of the fly head in an effort to understand the extent to which their organization is consistent with the parallel model of hierarchical suppression in the context of grooming behavior. They map the locations of the mechanosensory bristles on the fly head, examine the axonal morphology of the bristle mechanosensory neurons (BMNs) that innervate them, and match these to electron microscopy reconstructions of the same BMNs in a previously published EM volume of the female adult fly brain. They use BMN synaptic connectivity information to create clusters of BMNs that they show occupy different regions of the subesophageal zone brain region and use optogenetic activation of subsets of BMNs to evaluate the behaviors evoked by specific activation of BMN subpopulations innervating the head.

The authors have beautifully cataloged the mechanosensory bristles and the projection paths and patterns of the corresponding BMN axons in the brain using detailed and painstaking methods. The result is a neuroanatomy resource that will be an important community resource. To match BMNs reconstructed in an electron microscopy volume of the adult fly brain, the authors matched clustered reconstructed BMNs with light-level BMN classes observed using precise dye-fills and stochastic labeling techniques. The authors then employ a variety of clustering methods to demonstrate that BMN populations that innervate different regions of the head project into the subesophageal zone and terminate in distinctive yet, in some cases, partially overlapping zones. By clustering BMNs on the basis of their synaptic partners, the authors find that BMNs from distant areas of the head have non-overlapping synaptic partners while those from neighbor areas have overlapping synaptic partners. This result calls into question the scale at which the parallel model of hierarchical suppression may be operating. Finally, the authors use tools that were generated during the light-level characterization of BMN projections to show that activating BMNs that innervate specific areas of the head leads to grooming of the innervated regions and neighboring regions, consistent with the observed overlap in downstream circuits between BMNs innervating neighboring regions of the head. This result suggests that while the parallel model could be operating on a broad scale, additional circuit mechanisms may be operating on a finer scale to produce grooming of the area surrounding the source of mechanosensory input.

This work will have a positive impact on the field by contributing a complete accounting of the mechanosensory bristles of the fruit fly head, describing the brain projection patterns of the BMNs that innervate them, and linking them to BMN sensory projections in an electron microscopy volume of the adult fly brain. It will also have a positive impact on the field by providing genetic tools to help functionally subdivide the contributions of different BMN populations to circuit computations and behavior. This contribution will pave the way for further mechanistic study of central circuits that subserve grooming circuits.

Reviewer #2 (Public Review):

The authors address a question that is interesting and important to the sub-field of rsfMRI that examines electrophysiological correlates of rsfMRI. That is, while electrophysiology-produced correlation maps often appear similar to correlation maps produced from BOLD alone (as has been shown in many papers) is this actually coming from the same source of variance, or independent but spatially-correlated sources of variance? To address this, the authors recorded LFP signals in 2 areas (M1 and ACC) and compared the maps produced by correlating BOLD with them to maps produced by BOLD-BOLD correlations. They then attempt to remove various sources of variance and see the results.

The basic concept of the research is sound, though primarily of interest to the subset of rsfMRI researchers who use simultaneous electrophysiology. However, there are major problems in the writing, and also a major methodological problem.

Major problems with writing:

(1) There is substantial literature on rats on site-specific LFP recording compared to rsfMRI, and much of it already examined removing part of the LFP and examining rsfMRI, or vice versa. The authors do not cover it and consider their work on signal removal more novel than it is.

(2) The conclusion of the existence of an "electrophysiology-invisible signal" is far too broad considering the limited scope of this study. There are many factors that can be extracted from LFP that are not used in this study (envelope, phase, infraslow frequencies under 0.1Hz, estimated MUA, etc.) and there are many ways of comparing it to the rsfMRI data that are not done in this study (rank correlation, transformation prior to comparison, clustering prior to comparison, etc.). The one non-linear method used, mutual information, is low sensitivity and does not cover every possible nonlinear interaction. Mutual information is also dependent upon the number of bins selected in the data. Previous studies (see 1) have seen similar results where fMRI and LFP were not fully commensurate but did not need to draw such broad conclusions.

(3) The writing refers to the spatial extent of correlation with the LFP signal as "spatial variance." However, LFP was recorded from a very limited point and the variance in the correlation map does not necessarily reflect underlying electrophysiological spatial distributions (e.g. Yu et al. Nat Commun. 2023 Mar 24;14(1):1651.)

Major method problem:

(4) Correlating LFP to fMRI is correlating two biological signals, with unknown but presumably not uniform distributions. However, correlating CC results from correlation maps is comparing uniform distributions. This is not a fair comparison, especially considering that the noise added is also uniform as it was created with the rand() function in MATLAB.

eLife assessment

This valuable manuscript shows that the optogenetic stimulation of direct and indirect pathway spiny projection neurons (SPNs) in the dorsomedial versus the dorsolateral striatum has different consequences for locomotor activity, real-time place preference, and action selection, in a contextually mediated manner. The evidence in support of this conclusion is solid but would be further strengthened through deeper analysis of the effect and specificity of optogenetic manipulations on SPN activity. These findings will be of interest to neuroscientists, particularly behavioral neuroscientists.

Reviewer #1 (Public Review):

Summary:

The motivating questions are an accurate reflection of the current state of knowledge surrounding striatal pathway function. The comparisons of pathway function across striatal subregion, activation & inhibition, and task context are laudable and extremely important for advancing the subfield. Had these manipulations, to the largest extent possible been performed in single animals (e.g. activate dSPNs of DMS or DLS in the same mouse across the 3 tasks), this would have significantly strengthened the impact and conclusions that could be drawn by making this set of studies even more so internally consistent and directly comparable. While this is no longer possible, a conceptually related and fantastic contribution to the subfield (and likely beyond in terms of Opto manipulations of brain areas) would be to directly demonstrate that within their studies their DMS pathway manipulations do not impact nearby DLS activity (and vice versa). This is a significant and non-essential request. More feasibly and reasonably, it would be fantastic and strengthen the conclusions here to more fully detail their opsin expression patterns in DMS vs DLS groups and perhaps attempt to relate individual opsin profiles and fiberoptic targeting with behavioral outcomes across tests.

Strengths:

A comprehensive and paired comparison of inhibition and activation of striatal pathways across subregions and tasks is a very important and meaningful step towards reconciling contradictory results on striatal pathway function that are observed across labs (who typically focus on one subregion, one task setting, and often do not directly report comparisons of activation and inhibition).

Weaknesses:

Figure 1A - the example DMS vs DLS opsin expression and fiber targeting are not terribly convincing that the manipulations will be specific to each subregion (the example in Figure 2A is a little better but I have a similar concern still). The specificity of these manipulations is key to interpretation and conclusions and I strongly feel they should be strengthened here. The best evidence would be direct neural recordings (light in DMS, no effect in DLS, and vice versa), but this is a tall ask and not expected. The next best option, which is readily feasible, is to show not only fiberoptic targeting summaries (as in Figure 1A, Figure 2A) but also a summary of opsin spread for all animals (especially given the two examples appear to have significant spread across DMS and DLS). It would be of great benefit to the field to have these in the Allen Common Coordinate Framework. It would also be fine and useful to utilize the authors' current classical histological atlas alignment methods (e.g. Paxinos pdf). These histological summary figures would also benefit from being larger and more visible (perhaps as separate supplemental figures associated with the main figures).

Related to the above, it is a concern that the classic view is supported or not because of individual variations in virus/fiber targeting to striatal subregions which likely have greater granularity than the traditional dorsal medial vs lateral (e.g. Hunnicutt et al 2016, Foster et al 2021, Hintiryan et al 2016). Although there may not be enough animals or variation in targeting in the present study to find meaningful relationships, it would strengthen the paper and be a great benefit to the field to know whether for key findings if the strength of behavioral effects correlated with anterior/posterior or medial/lateral or dorsal/ventral fiberoptic coordinates (or the volume of opsin expression profiles).

Conceptually, a clear new idea or integrative interpretation of prior work (nor even the large body of results within this work) comes to the fore, save for the already appreciated fact that the classic view of opposing pathways is sometimes supported and sometimes not. Two tangible suggestions that I believe would facilitate the influence of this study - (1) can the authors more thoughtfully bridge the logical steps in their results sections and the prior context around them (some topic sentences jump right into results, e.g. line 195: "The inhibition experiment showed), and (2) in discussion, rather than emphasizing when/where the classic view is supported and not, more content on precisely why would be helpful. Some questions more specifically, if DMS/DLS pathway activation/inhibition is *mostly* oppositely appetitive/aversive, what does that mean in the context of spontaneous or reward-guided locomotion? Self-initiated pathway activation/inhibition is in part learned (with very intriguing differences across pathways in the expression across learning) - how should we think about striatal pathway function with regards to learning, spontaneous/innate behaviors, vs over-trained behaviors? When the classic view fails in the dorsal striatum - why? And is a complimentary "model" an actual alternative concept, a distinct mode of circuit function, or just a negative result on the classic view?

Reviewer #2 (Public Review):

Summary:

Cuevas et al. investigate the involvement of DMS and DLS direct and indirect pathways in locomotion and action selection using optogenetic manipulation techniques. They show that optical excitation of dSPNs in both DMS and DLS induces place preference, with optical inhibition resulting in the opposite effect. Interestingly, and somewhat not coming as a surprise given many previous data on this, optical excitation of iSPNs in both regions resulted in place aversion - in line with the classical view of functional opposition.

Then, the authors performed a two-choice task in which animals would have to choose between pressing in a lever alone or in a lever+stim to obtain a food reward. Again, and not surprisingly, they show that optical activation of dSPNs results in selection from pressing in the lever+stim with the opposite being observed for iSPN, in both DMS and DLS. What was concerting was the increase in lever pressing when inhibiting dSPNs in the DMS, since before authors show that it should cause aversion. When looking at locomotor effects, the authors report an increase in spontaneous displacement when exciting dSPNs in DMS, and the opposite in DLS. Contrary, the excitation of iSPNs either in DMS or DLS increased spontaneous displacement. In reward-seeking, displacement excitation of either dSPNs or iSPNs in both regions resulted in decreased locomotion.

Strengths:

Overall this manuscript brings a new light to the involvement of DLS SPNs in both locomotion and behavioral preference.

Weaknesses:

Some of the main claims would benefit from further discussion or new data on the effect of optogenetic manipulation on the activity of SPNs. This could allow for the creation of a clearer picture of the involvement of iSPNs and dSPNs of DMS and DLS for behavior.

eLife assessment

The authors of this study implemented an important toolset for 3D reconstruction and segmentation of dissection photographs, which could serve as an alternative for cadaveric and ex vivo MRIs. The tools were tested on synthetic and real data with compelling performance. This toolset could further contribute to the study of neuroimaging-neuropathological correlations.

Reviewer #1 (Public Review):

Gazula and co-workers presented in this paper a software tool for 3D structural analysis of human brains, using slabs of fixed or fresh brains. This tool will be included in Freesurfer, a well-known neuroimaging processing software. It is possible to reconstruct a 3D surface from photographs of coronal sliced brains, optionally using a surface scan as model. A high-resolution segmentation of 11 brain regions is produced, independent of the thickness of the slices, interpolating information when needed. Using this method, the researcher can use the sliced brain to segment all regions, without the need of ex vivo MRI scanning.

The software suite is freely available and includes 3 modules. The first accomplishes preprocessing steps, for correction of pixel sizes and perspective. The second module is a registration algorithm that registers a 3D surface scan obtained prior to sectioning (reference) to the multiple 2D slices. It is not mandatory to scan the surface, -a probabilistic atlas can also be used as reference- however the accuracy is lower. The third module uses machine learning to perform the segmentation of 11 brain structures in the 3D reconstructed volume. This module is robust, dealing with different illumination conditions, cameras, lens and camera settings. This algorithm ("Photo-SynthSeg") produces isotropic smooth reconstructions, even in high anisotropic datasets (when the in-plane resolution of the photograph is much higher than the thickness), interpolating the information between slices.

To verify the accuracy and reliability of the toolbox, the authors reconstructed 3 datasets, using real and synthetic data. Real data of 21 postmortem confirmed Alzheimer's disease cases from the Massachusetts Alzheimer's Disease Research Center (MADRC)and 24 cases from the AD Research at the University of Washington(who were MRI scanned prior to processing)were employed for testing. These cases represent a challenging real-world scenario. Additionally, 500 subjects of the Human Connectome project were used for testing error as a continuous function of slice thickness. The segmentations were performed with the proposed deep-learning new algorithm ("Photo-SynthSeg") and compared against MRI segmentations performed to "SAMSEG" (an MRI segmentation algorithm, computing Dice scores for the segmentations. The methods are sound and statistically showed correlations above 0.8, which is good enough to allow volumetric analysis. The main strengths of the methods are the datasets used (real-world challenging and synthetic) and the statistical treatment, which showed that the pipeline is robust and can facilitate volumetric analysis derived from brain sections and conclude which factors can influence in the accuracy of the method (such as using or not 3D scan and using constant thickness).

Although very robust and capable of handling several situations, the researcher has to keep in mind that processing has to follow some basic rules in order for this pipeline to work properly. For instance, fiducials and scales need to be included in the photograph, and the slabs should be photographed against a contrasting background. Also, only coronal slices can be used, which can be limiting for certain situations.

The authors achieved their aims, and the statistical analysis confirms that the machine learning algorithm performs segmentations comparable to the state-of-the-art of automated MRI segmentations.<br /> Those methods will be particularly interesting to researchers who deal with post-mortem tissue analysis and do not have access to ex vivo MRI. Quantitative measurements of specific brain areas can be performed in different pathologies and even in the normal aging process. The method is highly reproducible, and cost-effective since allows the pipeline to be applied by any researcher with small pre-processing steps.

Reviewer #2 (Public Review):

Summary

The authors proposed a toolset Photo-SynthSeg to the software FreeSurfer which performs 3D reconstruction and high-resolution 3D segmentation on a stack of coronal dissection photographs of brain tissues. To prove the performance of the toolset, three experiments were conducted, including volumetric comparison of brain tissues on AD and HC groups from MADRC, quantitative evaluation of segmentation on UW-ADRC and quantitative evaluation of 3D reconstruction on HCP digitally sliced MRI data.

Strengths

To guarantee the successful workflow of the toolset, the authors clearly mentioned the prerequisites of dissection photograph acquisition, such as fiducials or rulers in the photos and tissue placement of brain slices with more than one connected component. The quantitative evaluation of segmentation and reconstruction on synthetic and real data demonstrates the accuracy of the methodology. Also, the successful application of this toolset on two brain banks with different slice thicknesses, tissue processing and photograph settings demonstrates its robustness. By working with tools of the SynthSeg pipeline, Photo-SynthSeg could further support volumetric cortex parcellation. The toolset also benefits from its adaptability of different 3D references, such as surface scan, ex vivo MRI and even probabilistic atlas, suiting the needs for different brain banks.

Weaknesses

Certain weaknesses are already covered in the manuscript. Cortical tissue segmentation could be further improved. The quantitative evaluation of 3D reconstruction is quite optimistic due to random affine transformations. Manual edits of slice segmentation task are still required and take a couple of minutes per photograph. Finally, the current toolset only accepts coronal brain slices and should adapt to axial or sagittal slices in future work.

Author Response

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

Reviewer #1

Weaknesses:

Start site fidelity in purified recons5tuted systems can be drama5cally altered in different buffer condi5ons. Interpreta5on of the observed changes to start site selec5on in mRNAs in the absence or presence of Ded1 using only the one buffer condi5on used is therefore limited.

This is an excellent point and is something we could explore in future studies using the Rec-Seq system. We have added this caveat to the Discussion on lines 797-809. We have previously studied the fidelity of start codon recogni>on in the recons>tuted system (Kolitz et al., [2009] RNA, 15:138-152) and found that under our standard buffer condi>ons the codon specificity generally reflects what we observed in vivo using a dual-luciferase reporter assay, with the most stable 48S complexes forming on AUG codons, followed by first posi>on mismatches (GUG, UUG, CUG), with second and third posi>on mismatches leading to significantly less stable complexes. However, as the reviewer notes, there are some devia>ons: ACG and AUA are poor codons in the in vitro system under the buffer condi>ons used but allowed rela>vely strong expression in our in vivo reporter assay. It should also be noted that the hierarchy of nearcognate start codon usage in vivo in yeast differs according to the study and the reporter used, making it difficult to establish a “ground truth” for start codon fidelity.

I have some specific comments to strengthen the manuscript and address some minor issues.

It is not clear to me whether the authors refold the purified mRNA aEer phenol/chloroform extrac5on? Have the authors observed different results if the mRNA is refolded or not? This is appropriate since the authors compare their Rec-Seq data to PARS scores that were generated from refolded mRNAs. One assumes that the total mRNA used is refolded in the same way as the PARS score study, but this is not clearly stated. The authors should make this point clear in the text and methods.

This is an excellent point. We did not use the final refolding protocol that Kertesz et al. used when they developed their PARS scores and now clarify this in the Methods sec>on (lines 962967). It is possible that we would have seen stronger correla>ons in the analyses using PARS scores had we followed the renatura>on protocol, although the fact that we observed significant correla>ons (e.g., Fig. 3E-H) suggests the structures in the Kertesz et al. mRNAs were similar to those in our mRNAs.

It is not clear how the authors determine the concentra5on of total mRNA that is used in the assay - reported as 60 nM? Are the authors assuming a molecular weight of an average mRNA to determine the concentra5on? The authors should provide more detail for how they quan5fy their mRNA concentra5on and its stoichiometry compared to 43S PICs.

We thank the reviewer for poin>ng out this oversight and have now included this informa>on on lines 849-855 of the Methods sec>on.

Comments regarding start site fidelity in the recons5tuted system:

The authors use in vitro transcribed tRNAi-Met. Since tRNA modifica5ons may play a role in start site fidelity, the authors should perhaps men5on that this will need to be inves5gated in a future study in the discussion.

This is a good point and we now note it as a caveat in the Discussion on lines 806-809.

The authors state that Ded1 promotes leaky scanning regardless of the mAUG start site context (page 24; lines 533-534). The authors then state on page 25 that the level of iAUG ini5a5on rela5ve to mAUG ini5a5on does depend on the mAUG context (lines 545-546). This seems contradictory unless I am not understanding this correctly? It would certainly be surprising that mAUG context didn't regulate leaky scanning in the recons5tuted system given the fact that ini5a5on codon context regulates selec5on in cells (when Ded1 is present).

These statements are correct as wrihen. As shown in Figure 5O, the frequency of leaky scanning (as measured by rela>ve ribosome occupancy of the internal region of the ORF, not including the main start codon, to the whole ORF, including the main start codon; RRO) decreases as the context score around the start codon gets stronger (green and purple lines). The RRO is increased to the same extent when 500 nM Ded1 is added, regardless of the strength of the start codon context, indica>ng that Ded1 enhances leaky scanning equally (compare slopes of the green line without Ded1 to the purple line with Ded1). Because of this, the effect of Ded1 on RRO (DRR0) is constant across context score bins (orange line). There is no discrepancy between our two conclusions that leaky scanning of the mAUG increases as context score decreases and that Ded1 increases leaky scanning equally for good and bad mAUG contexts, indica>ng that Ded1 does not inspect the mAUG context and simply decreases the dwell >me equally at all contexts.

Further to the start site context ques5on. It is possible that the fidelity of the recons5tuted system (i.e. buffer condi5ons) is not fully reflec5ng in vivo-like start site selec5on. A rigorous characteriza5on of commercially available re5culocyte lysate systems iden5fied buffer condi5ons that provided similar start site fidelity to that observed in live cells (Kozak. Nucleic Acids Res. 1990 May 11;18(9):2828). While I feel that it is beyond the context of the current work to undertake a similar rigorous buffer characteriza5on, one must be careful about interpre5ng the results about leaky scanning and upstream ini5a5on sites in the current work. Perhaps one would observe similar results to Guenther et al. if the fidelity (buffer condi5ons) of the recons5tuted system were different? I appreciate that the authors state that their results only apply to their recons5tuted system and do not necessarily suggest that previous data are incorrect, but with only one buffer condi5on being tested in the current study it may be appropriate to further soEen the interpreta5on of the current results when compared to published data in live cells.

This point is well-taken. As noted above, we have added a caveat about possible effects of buffer condi>ons on start codon fidelity to the Discussion (lines 797-809). In terms of the possibility that upstream ini>a>on is more frequent in vivo than we observe in the in vitro RecSeq system, we previously studied 5’UTR transla>on in vivo using ribosome profiling (Kulkarni et al. [2019] BMC Biol., 17:101). The ra>o of RPFs in 5’UTRs to coding sequences in this study was 0.0027, very similar to the value measured in the in vitro Rec-Seq system in the presence of Ded1 (0.0016-0.0017). Thus, it does not seem that the frequency of upstream ini>a>on is drama>cally higher in vivo than in our in vitro system. We have now made note of this point in the Results (lines 594-598). Guenther et al. employed a ribosome profiling protocol in which they added cycloheximide to their cells prior to lysis, which has been shown to create significant ar>facts, par>cularly in 5’UTR transla>on (e.g., Gerashchenko and Gladyshev [2014] Nucleic Acids Res., 42:e134). Nevertheless, as suggested by the reviewer, we have modified the text in the Results and Discussion to somen the interpreta>on somewhat (lines 582-583; 616-618; 761763).

Reviewer #2

Weaknesses:

Several findings in this report are quite surprising and may require addi5onal work to fully interpret. Primary among these is the finding that Ded1p s5mulates accumula5on of PICs at internal site in mRNA coding sequences at an incidence of up to ~50%. The physiological relevance of this is unclear.

We agree with the reviewer that understanding the physiological significance, if any, of the apparent leaky scanning of main AUG start codons induced by Ded1 is an unanswered ques>on that will require addi>onal studies. It is possible that rapid 60S subunit joining and forma>on of the 80S ini>a>on complex amer start codon recogni>on on most mRNAs reduces the leaky scanning effect in vivo. We now bring up this possibility in the Discussion sec>on (lines 804809). However, as noted in lines 568-580, mRNAs that display significantly decreased mRPFs at 500 nM Ded1 in the Rec-Seq system also tend to have TEs that are increased in the ded1-cs- mutant rela>ve to WT yeast in in vivo ribosome profiling experiments, sugges>ng that Ded1 ac>vity also diminishes ini>a>on on mAUG codons in these mRNAs in vivo.

A limita5on of the methodology is that, as an endpoint assay, Rec-Seq does not readily decouple effects of Ded1p on PIC-mRNA loading from those on the subsequent scanning step where the PIC locates the start codon. Considering that Ded1p ac5vity may influence each of these ini5a5on steps through dis5nct mechanisms - i.e., binding to the mRNA cap-recogni5on factor eIF4F, or direct mRNA interac5on outside eIF4F - addi5onal studies may be needed to gain deeper mechanis5c insights.

We agree that this is a limita>on of the Rec-Seq assay and now men>on this point in the Discussion sec>on (lines 810-817). It is possible that future work using cross-linking agents to stabilize 43S complexes bound near the cap and scanning the 5’UTR, similar to the methodology used in 40S ribosome profiling, could enable us or others to disentangle these steps from one another.

As the authors note, the achievable Ded1p concentra5ons in Rec-Seq may mask poten5al effects of Ded1p-based granule forma5on on transla5on ini5a5on. Addi5onal factors present in the cell could poten5ally also promote this mechanism. Consequently, the results do not fully rule out granule forma5on as a poten5al parallel Ded1p-mediated transla5on-inhibitory mechanism in cells.

We agree. As stated in the Discussion sec>on (lines 735-741): “It is possible that at higher concentra>ons of Ded1 than were achievable in these in vitro experiments or in the presence of addi>onal factors that modify Ded1’s ATPase or RNA binding ac>vi>es the factor could directly inhibit a subset of mRNAs, by ac>ng as an mRNA clamp that impedes scanning by the PIC, or by sequestering the mRNAs in insoluble condensates. It might be interes>ng in the future to test candidate factors in Rec-Seq to determine if they switch Ded1 from being a s>mulatory helicase to an inhibitory mRNA clamp that removes transcripts from the soluble phase.”

It is certainly clear why the 15-minute 5mepoint was chosen for these assays. However, I wondered whether data from an earlier 5mepoint would provide useful informa5on. The descrip5on on line 210 of the compiled PDF suggests data from different 5mepoints may be available; if it is, in my view it could be a useful addi5on. More generally, including language about the single-turnover nature of these reac5ons may be helpful for the benefit of a broad audience.

In preliminary experiments, we have used the Rec-Seq system to measure the kine>cs of 48S PIC forma>on transcriptome-wide. As you probably can imagine, this is a challenging experiment and requires addi>onal work before we would feel comfortable publishing it. We very much agree with the reviewer that resolving the kine>cs of these events will provide important addi>onal informa>on. As suggested, we have added caveats about the endpoint and single-turnover nature of the assay to the Discussion (lines 821-828).

I wondered whether it might be useful to present addi5onal informa5on on the mRNAs not found in the assay. For example, are these the least abundant mRNAs, which may not have had 5me to recruit the 43S PIC?

75% of mRNAs (2719 of 3640) not observed in the Rec-Seq analysis had densi>es below the median (2.3 reads per nucleo>de). We now men>on this in the Methods sec>on (lines 855856).

The Rec-Seq recruitment reac5ons were carried out at 22C˚ . Considering that remodeling of RNA structure by helicase enzymes is a focal point of the study, linking the results to the recruitment landscape at a closer-to-physiological temperature may bolster the conclusions.

In the future, it would be interes>ng to test the effects of temperature on 48S PIC forma>on using the Rec-Seq system. As the reviewer suggests, the interplay between temperature and mRNA structure could reveal interes>ng phenomenon. It is worth no>ng, however, that there is no clear “physiological” temperature for S. cerevisiae. For consistency and convenience, lab yeast is usually grown at 30 ˚C, but in the wild yeast live at a wide range of temperatures, which generally change throughout the day. From this standpoint, 22 ˚C seems reasonably physiological.

Results from Rec-seq experiments conducted at 15° C might be more directly comparable to in vivo Ribo-seq data with the ded1-cs mutant. However, already ~90% of the Ded1hyperdependent mRNAs iden>fied by Ribo-seq analysis of that mutant were iden>fied here as Ded1-s>mulated mRNAs in Rec-Seq experiments at 22°C. The Ribo-seq experiments conducted by Guenther et al. were conducted on the ded1-ts mutant at 37°C; thus, any structures that confer Ded1-dependent leaky-scanning through uORFs detected in that study should have been stable in our Rec-Seq experiments.

The introduc5on provides an important, detailed exposi5on of the state of the field with respect to Ded1p ac5vity. Nevertheless, in my view, it is quite lengthy and could be streamlined for clarity. As just one example, the proposed func5on of Ded1p in the nucleus seems like a detail that could be dispensed with for the present work.

We have ahempted to shorten the Introduc>on, as suggested. However, we did not remove the short sec>on describing Ded1’s possible roles in the nucleus and ribosome biogenesis because we felt it was important to emphasize that one of the strengths of the Rec-Seq system is that it allows us to isolate the early steps of transla>on ini>a>on from later steps and from other cellular processes. In addi>on, at the sugges>on of Reviewer #3, we added a brief explana>on of Ded1’s possible role in the subunit joining step of transla>on.

Reviewer #3

Weaknesses:

The slow nature of the biochemical experiments could bias results.

We agree that the 15-minute >me point used could mask effects that are manifested at a purely kine>c level. It should be noted that we have measured the observed rate constants for 48S forma>on on a variety of mRNAs in the in vitro recons>tuted system in the presence of satura>ng Ded1 (Gupta et al. [2018] eLife, hhps://elifesciences.org/ar>cles/38892 ) and found that they are generally in the range of es>mates of rate constants for transla>on ini>a>on in vivo in yeast (~1-10 min-1; e.g., Siwiak and Zielenkiewicz [2010], PLOS Comput. Biol., 6: e100865). In preliminary experiments, we have used the Rec-Seq system to measure the kine>cs of 48S PIC forma>on transcriptome-wide in the absence of Ded1 and find that the mean rate constant observed (~2 min-1) is also within the range of es>mates of the rate of transla>on ini>a>on in vivo in yeast. We hope to publish this analysis in a future manuscript.

It has been suggested that Ded1 and its human homolog DDX3X could play a role in subunit joining postscanning (Wang et al. 2022, Cell and Geissler et al. 2012 Nucleic Acids Res). Could the authors poten5ally inves5gate this by adding GTP, eIF5B and 60S subunits into the reac5on mixture and isola5ng 80S complexes?

This is a very interes>ng sugges>on. One of our plans with the Rec-Seq system is to see if we can also observe 80S forma>on with it and dis>nguish 80S from 48S complexes. Although we haven’t yet tried this and there might be technical obstacles to doing it, if it works we would like to examine the poten>al effects of Ded1, as suggested. We now men>on this possibility in the Discussion sec>on (lines 709-716 and 810-817).

An incuba5on 5me of 15 minutes is quite long on the 5mescale of transla5on ini5a5on. Presumably, the compe55on for 40S among mRNAs is par5ally kine5cally controlled so it would be interes5ng if the authors could do a 5me series on the incuba5on 5me. Does Ded1 increase ini5a5on on more structured UTRs even at shorter incuba5ons or are those only observed with longer incuba5ons?

We agree. See the response to the ques5on about kine5cs above.

Does GDPNP lead to off-pathway events? What happens when GTP is used in the TC? Presumably in the absence of eIF5B the 48S PIC should remain stalled at the start codon.

In previous experiments in the recons>tuted system, we showed that using GTP instead of GDPNP resulted in 48S complexes that were less stable than those stalled prior to GTP hydrolysis (e.g., Algire et al. [2002] RNA 8:382-397). This is presumably because eIF2•GDP and eIF5 release from the complex and the Met-tRNAi can dissociate in the absence of subunit joining. Although we haven’t tried it in the Rec-Seq system, we suspect that the resul>ng PICs would fall apart during sucrose gradient sedimenta>on.

The authors use assembly of a 48S PIC at the start codon as evidence of scanning but could use more evidence to back this claim up. Does removing the cap structure on the two luciferase mRNA controls disrupt ini5a5on using this approach? That would be direct evidence of 5' end 40S loading and scanning to the start codon.

In previous work using the recons>tuted system, we studied the effect of the 5’-cap on 48S PIC forma>on (Mitchell et al. [2010] Mol. Cell 39:950-962; Yourik et al. [2017] eLife hhps://elifesciences.org/ar>cles/31476 ). We found that stable 48S PIC forma>on is strongly dependent on the presence of the 5’-cap. In addi>on, the cap prevents off-pathway events and enforces a requirement for the full set of ini>a>on factors to achieve efficient 48S PIC forma>on. As the reviewer indicates, the cap-dependence of the system supports the conclusion that 5’end loading and scanning take place. We have now added this informa>on and the relevant cita>ons to the Introduc>on (lines 147-153). We thank the reviewer for poin>ng out this oversight. It should also be noted that the cases of mRNAs in which 5’UTR transla>on is increased by addi>on of Ded1 support the conclusion that the factor promotes ahachment of the PIC to the 5’ ends of mRNAs and subsequent 5’ to 3’ scanning, as noted in lines 608-618.

The authors state that "The correla5on between CDS length and RE could be indirect because CDS length also correlates with 5'UTR length". Could the authors bin the transcripts into different 5' UTR length ranges and then probe for CDS length differences on RE for each 5' UTR length bin? This could be useful to truly parse the mechanism by which CDS length is influencing RE.

This was an excellent sugges>on. We now include this analysis in a new supplementary figure, Figure 3S-2. Corresponding text was added in lines 380-387:

“Importantly, correlations between Ded1 stimulation and 5’ UTR lengths are evident for all three groups of mRNAs containing distinct ranges of CDS lengths (Fig. 3-S2A-C). In contrast, a marked correlation between Ded1 stimulation and CDS length was detected only for the group of mRNAs with longest 5’UTRs (Fig. 3-S2D-F), and only the latter group showed a clear correlation between 5’UTR length and CDS length (Fig. 3-S2G-I). Thus, the correlation between Ded1 stimulation and CDS length appears to be indirect, driven by the tendency for the mRNAs with the longest 5’UTRs to also have correspondingly longer CDSs.”

We thank the reviewer for this very useful idea.

In Figure 3I, why does RE dip for the middle bins of CDS length in both 100 nM and 500 nM condi5ons, and then rise back up for the later bins? In other words, why do the shortest and longest CDS have the best RE in the presence of ded1?

We do not know the reason for this dip and now say this in the Results on lines 377-378.

The discussion sec5on would be well served to discuss proposed roles of Ded1 post-scanning and how those fit, if at all, with the data presented throughout the manuscript.

We have now added this to the Discussion (lines 709-716 and 810-817). We thank the reviewer for poin>ng out this oversight.

Minor comments:

• Define bins on figures rather than using bin number for axis labels. For example, Figure 3A-D x-axis labels indicate the length range of each bin.

Thank you for the sugges>on. We have made this change.

• Figure 3I: the data seem to indicate that shortest CDSs have a ded1 dependency similar to the longest CDSs. This result seems inconsistent with the given rela5onship between UTR length, structure, CDS length. Please clarify.

See answer to this ques>on above.

• Replace qualita5ve statements, such as "substan5ally smaller reduc5ons" with percent change, numbers, etc.

We have tried to replace qualita>ve statements with quan>ta>ve ones, where possible.

eLife assessment

This is an important paper as it is the first to use a reconstituted translation system to study competition among mRNAs for the initiation machinery. Understanding the principles of the biochemistry of mRNA competition for initiation factors cannot be achieved without such a system. The authors provide compelling evidence that Ded1 is required for efficient initiation of highly structured mRNAs. The findings are significant and validate the in vitro reconstituted system by recapitulating the effects of in-vivo perturbations of translation initiation by Ded1 mutants.

Reviewer #1 (Public Review):

The authors have developed and optimized a footprinting assay to monitor the recruitment of mRNAs to a reconstituted translation initiation system. This assay is named Recruitment-Sequencing (Rec-Seq) and enables the analysis of many purified mRNAs in the reconstituted system.

This system possesses the ability to determine how competition occurs between mRNAs for the initiation machinery. This is the first approach using a reconstituted system that enables this important feature, and this is an important advance for the field.

Using purified mRNAs in a fully reconstituted system together with the ability to monitor start site selection is an important advance. The method enables one to observe for the first time how competition between mRNAs is altered in response to the absence or presence of different initiation components or accessory proteins.

Start site fidelity in purified reconstituted systems can be altered in different buffer conditions and by the concentration of various initiation factors involved in start site fidelity. Future experiments will reveal how these variables can regulate start site selection in this powerful system.

Comments on revised version:

The authors have addressed all of my original comments. This is an impressive manuscript.

Reviewer #2 (Public Review):

Summary:

Zhou et al report development of a new method, Rec-Seq, that allows rigorous quantitation of the efficiency of 48S ribosomal pre-initiation complex (PIC) formation on messenger RNAs at transcriptome scale in vitro. With a next-generation deep-sequencing approach, Rec-Seq allows precisely targeted dissection of the roles of translation initiation factors in PIC assembly. This level of molecular precision is important to understanding mechanisms of translational control, making Rec-Seq a significant methodological advance. The authors leverage Rec-Seq to investigate the relative roles of two key helicase enzymes, Ded1p and eIF4A. While past work has pointed to differing roles for Ded1p and eIF4A helicase activity in PIC assembly, unambiguous interpretation of prior in-vivo data has been hindered by technical requirements for performing the experiments in cells. Rec-Seq circumvents these challenges, providing robust mechanistic insights. The authors find that Ded1p stimulates PIC formation selectively on mRNAs with long, structured leaders in the Rec-Seq system, while eIF4A provides much more general stimulation across mRNAs. The findings substantiate the past in-vivo results, along with adding new insights. They contrast with evidence that Ded1p promotes translation by suppressing inhibitory upstream initiation through structural remodeling, or through formation of intracellular, phase-separated granules. The conclusions of the study are well-supported by the data, and are likely to be of broad interest.

Strengths:

The quantitative nature of Rec-Seq, which uses an internal standard to measure absolute recruitment efficiencies, is an important strength.

The methodology decisively overcomes past experimental limitations, allowing the authors to make clear conclusions with regard to the relative roles of Ded1p and eIF4A in PIC formation. An important and useful addition to the toolbox for studying translation and translational control mechanisms, Rec-Seq substantially expands the throughput and scope of mechanistic analyses for translation initiation.

One significant finding to emerge is that the in-vitro reconstituted system used here recapitulates effects of in-vivo perturbations of translation initiation. Despite the lack of a cellular environment and its components, PIC formation appears to operate much as it does in the cell. Importantly, this highlights an inherent "modularity" to the system that is especially of interest in the context of how regulatory machinery beyond the PIC may control translation.

Weaknesses:

The study finds that Ded1p stimulates accumulation of PICs at internal AUG codons, i.e., within mRNA coding sequences, at an incidence of up to ~50% - thus, bypassing "canonical" translation start sites. Understanding the physiological significance of this activity will require further study. The authors address this in the text.

A limitation of the methodology is that, as an endpoint assay, Rec-Seq does not readily decouple effects of Ded1p on PIC-mRNA loading from those on the subsequent scanning step where the PIC locates the start codon. Considering that Ded1p activity may influence each of these initiation steps through distinct mechanisms - i.e., binding to the mRNA cap-recognition factor eIF4F, or direct mRNA interaction outside eIF4F - additional studies will be needed to gain deeper mechanistic insights. The authors discuss this in the text.

Comments on revised version:

In revising their manuscript, the authors have responded very thoughtfully and insightfully to the initial review. The final manuscript is an important contribution to the field, and I am sure it will be of broad interest.

Author Response

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

eLife assessment

This important study identifies the mitotic localization mechanism for Aurora B and INCENP (parts of the chromosomal passenger complex, CPC) in Trypanosoma brucei. The mechanism is different from that in the more commonly studied opisthokonts and there is solid support from RNAi and imaging experiments, targeted mutations, immunoprecipitations with crosslinking/mass spec, and AlphaFold interaction predictions. The results could be strengthened by biochemically testing proposed direct interactions and demonstrating that the targeting protein KIN-A is a motor. The findings will be of interest to parasitology researchers as well as cell biologists working on mitosis and cell division, and those interested in the evolution of the CPC.

We thank the editor and the reviewers for their thorough and positive assessment of our work and the constructive feedback to further improve our manuscript. Please find below our responses to the reviewers’ comments. Please note that the conserved glycine residue in the Switch II helix in KIN-A was mistakenly labelled as G209 in the original manuscript. We now corrected it to G210 in the revised manuscript.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The CPC plays multiple essential roles in mitosis such as kinetochore-microtubule attachment regulation, kinetochore assembly, spindle assembly checkpoint activation, anaphase spindle stabilization, cytokinesis, and nuclear envelope formation, as it dynamically changes its mitotic localization: it is enriched at inner centromeres from prophase to metaphase but it is relocalized at the spindle midzone in anaphase. The business end of the CPC is Aurora B and its allosteric activation module IN-box, which is located at the C-terminal part of INCENP. In most well-studied eukaryotic species, Aurora B activity is locally controlled by the localization module of the CPC, Survivin, Borealin, and the N-terminal portion of INCENP. Survivin and Borealin, which bind the N terminus of INCENP, recognize histone residues that are specifically phosphorylated in mitosis, while anaphase spindle midzone localization is supported by the direct microtubule-binding capacity of the SAH (single alpha helix) domain of INCENP and other microtubule-binding proteins that specifically interact with INCENP during anaphase, which are under the regulation of CDK activity. One of these examples includes the kinesin-like protein MKLP2 in vertebrates.

Trypanosoma is an evolutionarily interesting species to study mitosis since its kinetochore and centromere proteins do not show any similarity to other major branches of eukaryotes, while orthologs of Aurora B and INCENP have been identified. Combining molecular genetics, imaging, biochemistry, cross-linking IP-MS (IP-CLMS), and structural modeling, this manuscript reveals that two orphan kinesin-like proteins KIN-A and KIN-B act as localization modules of the CPC in Trypanosoma brucei. The IP-CLMS, AlphaFold2 structural predictions, and domain deletion analysis support the idea that (1) KIN-A and KIN-B form a heterodimer via their coiled-coil domain, (2) Two alpha helices of INCENP interact with the coiled-coil of the KIN-A-KIN-B heterodimer, (3) the conserved KIN-A C-terminal CD1 interacts with the heterodimeric KKT9-KKT11 complex, which is a submodule of the KKT7-KKT8 kinetochore complex unique to Trypanosoma, (4) KIN-A and KIN-B coiled-coil domains and the KKT7-KKT8 complex are required for CPC localization at the centromere, (5) CD1 and CD2 domains of KIN-A support its centromere localization. The authors further show that the ATPase activity of KIN-A is critical for spindle midzone enrichment of the CPC. The imaging data of the KIN-A rigor mutant suggest that dynamic KIN-A-microtubule interaction is required for metaphase alignment of the kinetochores and proliferation. Overall, the study reveals novel pathways of CPC localization regulation via KIN-A and KIN-B by multiple complementary approaches.

Strengths:

The major conclusion is collectively supported by multiple approaches, combining site-specific genome engineering, epistasis analysis of cellular localization, AlphaFold2 structure prediction of protein complexes, IP-CLMS, and biochemical reconstitution (the complex of KKT8, KKT9, KKT11, and KKT12).

We thank the reviewer for her/his positive assessment of our manuscript.

Weaknesses:

• The predictions of direct interactions (e.g. INCENP with KIN-A/KIN-B, or KIN-A with KKT9-KKT11) have not yet been confirmed experimentally, e.g. by domain mutagenesis and interaction studies.

Thank you for this point. It is true that we do not have evidence for direct interactions between KIN-A with KKT9-KKT11. However, the interaction between INCENP with KIN-A/KIN-B is strongly supported by our cross-linking IP-MS of native complexes. Furthermore, we show that deletion of the INCENPCPC1 N-terminus predicted to interact with KIN-A:KIN-B abolishes kinetochore localization.

• The criteria used to judge a failure of localization are not clearly explained (e.g., Figure 5F, G).

As suggested by the reviewer in recommendation #14, we have now included example images for each category (‘kinetochores’, ‘kinetochores + spindle’, ‘spindle’) along with a schematic illustration in Fig. 5F.

• It remains to be shown that KIN-A has motor activity.

We thank the reviewer for this important comment. Indeed, motor activity remains to demonstrated using an in vitro system, which is beyond the scope of this study. What we show here is that the motor domain of KIN-A effectively co-sediments with microtubules and that spindle localization of KIN-A is abolished upon deletion of the motor domain. Moreover, mutation of a conserved Glycine residue in the Switch II region (G210) to Alanine (‘rigor mutation’, (Rice et al., 1999)), renders KIN-A incapable of translocating to the central spindle, suggesting that its ATPase activity is required for this process. To clarify this point in the manuscript, we have replaced all instances, where we refer to ‘motor activity’ of KIN-A with ‘ATPase activity’ when referring to experiments performed using the KIN-A rigor mutant. In addition, we have included a Multiple Sequence Alignment (MSA) of KIN-A and KIN-B from different kinetoplastids with human Kinesin-1, human Mklp2 and yeast Klp9 in Figure 6A and S6A, showing the conservation of key motifs required for ATP coordination and tubulin interaction. In the corresponding paragraph in the main text, we describe these data as follows:

‘We therefore speculated that anaphase translocation of the kinetoplastid CPC to the central spindle may involve the kinesin motor domain of KIN-A. KIN-B is unlikely to be a functional kinesin based on the absence of several well-conserved residues and motifs within the motor domain, which are fully present in KIN-A (Li et al., 2008). These include the P-loop, switch I and switch II motifs, which form the nucleotide binding cleft, and many conserved residues within the α4-L12 elements, which interact with tubulin (Fig. S6A) (Endow et al., 2010). Consistent with this, the motor domain of KIN-B, contrary to KIN-A, failed to localize to the mitotic spindle when expressed ectopically (Fig. S2E) and did not co-sediment with microtubules in our in vitro assay (Fig. S6B).’

• The authors imply that KIN-A, but not KIN-B, interacts with microtubules based on microtubule pelleting assay (Fig. S6), but the substantial insoluble fractions of 6HIS-KINA and 6HIS-KIN-B make it difficult to conclusively interpret the data. It is possible that these two proteins are not stable unless they form a heterodimer.

This is indeed a possibility. We are currently aiming at purifying full-length recombinant KIN-A and KIN-B (along with the other CPC components), which will allow us to perform in vitro interaction studies and to investigate biochemical properties of this complex (including the role of the motor domains of KIN-A and KIN-B) within the framework of an in-depth follow-up study. To address the point above, we have added the following text in the legend corresponding to Fig. S6:

‘Microtubule co-sedimentation assay with 6HIS-KIN-A2-309 (left) and 6HIS-KIN-B2-316 (right). S and P correspond to supernatant and pellet fractions, respectively. Note that both constructs to some extent sedimented even in the absence of microtubules. Hence, lack of microtubule binding for KIN-B may be due to the unstable non-functional protein used in this study.’

• For broader context, some prior findings should be introduced, e.g. on the importance of the microtubule-binding capacity of the INCENP SAH domain and its regulation by mitotic phosphorylation (PMID 8408220, 26175154, 26166576, 28314740, 28314741, 21727193), since KIN-A and KIN-B may substitute for the function of the SAH domain.

We have modified the introduction to include the following text and references mentioned by the reviewer: ‘The localization module comprises Borealin, Survivin and the N-terminus of INCENP, which are connected to one another via a three-helical bundle (Jeyaprakash et al., 2007, 2011; Klein et al., 2006). The two modules are linked by the central region of INCENP, composed of an intrinsically disordered domain and a single alpha helical (SAH) domain. INCENP harbours microtubule-binding domains within the N-terminus and the central SAH domain, which play key roles for CPC localization and function (Samejima et al., 2015; Kang et al., 2001; Noujaim et al., 2014; Cormier et al., 2013; Wheatley et al., 2001; Nakajima et al., 2011; Fink et al., 2017; Wheelock et al., 2017; van der Horst et al., 2015; Mackay et al., 1993).’

Reviewer #2 (Public Review):

How the chromosomal passenger complex (CPC) and its subunit Aurora B kinase regulate kinetochore-microtubule attachment, and how the CPC relocates from kinetochores to the spindle midzone as a cell transitions from metaphase to anaphase are questions of great interest. In this study, Ballmer and Akiyoshi take a deep dive into the CPC in T. brucei, a kinetoplastid parasite with a kinetochore composition that varies greatly from other organisms.

Using a combination of approaches, most importantly in silico protein predictions using alphafold multimer and light microscopy in dividing T. brucei, the authors convincingly present and analyse the composition of the T. brucei CPC. This includes the identification of KIN-A and KIN-B, proteins of the kinesin family, as targeting subunits of the CPC. This is a clear advancement over earlier work, for example by Li and colleagues in 2008. The involvement of KIN-A and KIN-B is of particular interest, as it provides a clue for the (re)localization of the CPC during the cell cycle. The evolutionary perspective makes the paper potentially interesting for a wide audience of cell biologists, a point that the authors bring across properly in the title, the abstract, and their discussion.

The evolutionary twist of the paper would be strengthened 'experimentally' by predictions of the structure of the CPC beyond T. brucei. Depending on how far the authors can extend their in-silico analysis, it would be of interest to discuss a) available/predicted CPC structures in well-studied organisms and b) structural predictions in other euglenozoa. What are the general structural properties of the CPC (e.g. flexible linkers, overall dimensions, structural differences when subunits are missing etc.)? How common is the involvement of kinesin-like proteins? In line with this, it would be good to display the figure currently shown as S1D (or similar) as a main panel.

We thank the reviewer for her/his encouraging assessment of our manuscript and the appreciation on the extent of the evolutionary relevance of our work. As suggested, we have moved the phylogenetic tree previously shown in Fig. S1D to the main Fig. 1F. Our AF2 analysis of CPC proteins and (sub)complexes from other kinetoplastids failed to predict reliable interactions among CPC proteins except for that between Aurora B and the IN box. It therefore remains unclear whether CPC structures are conserved among kinetoplastids. Because components of CPC remain unknown in other euglenozoa (other than Aurora B and INCENP), we cannot perform structural predictions of CPC in diplonemids or euglenids.

It remains unclear how common the involvement of kinesin-like proteins with the CPC is in other eukaryotes, partly because we could not identify an obvious homolog of KIN-A/KIN-B outside of kinetoplastids. Addressing this question would require experimental approaches in various eukaryotes (e.g. immunoprecipitation and mass spectrometry of Aurora B) as we carried out in this manuscript using Trypanosoma brucei.

Reviewer #3 (Public Review):

Summary:

The protein kinase, Aurora B, is a critical regulator of mitosis and cytokinesis in eukaryotes, exhibiting a dynamic localisation. As part of the Chromosomal Passenger Complex (CPC), along with the Aurora B activator, INCENP, and the CPC localisation module comprised of Borealin and Survivin, Aurora B travels from the kinetochores at metaphase to the spindle midzone at anaphase, which ensures its substrates are phosphorylated in a time- and space-dependent manner. In the kinetoplastid parasite, T. brucei, the Aurora B orthologue (AUK1), along with an INCENP orthologue known as CPC1, and a kinetoplastid-specific protein CPC2, also displays a dynamic localisation, moving from the kinetochores at metaphase to the spindle midzone at anaphase, to the anterior end of the newly synthesised flagellum attachment zone (FAZ) at cytokinesis. However, the trypanosome CPC lacks orthologues of Borealin and Survivin, and T. brucei kinetochores also have a unique composition, being comprised of dozens of kinetoplastid-specific proteins (KKTs). Of particular importance for this study are KKT7 and the KKT8 complex (comprising KKT8, KKT9, KKT11, and KKT12). Here, Ballmer and Akiyoshi seek to understand how the CPC assembles and is targeted to its different locations during the cell cycle in T. brucei.

Strengths & Weaknesses:

Using immunoprecipitation and mass-spectrometry approaches, Ballmer and Akiyoshi show that AUK1, CPC1, and CPC2 associate with two orphan kinesins, KIN-A and KIN-B, and with the use of endogenously expressed fluorescent fusion proteins, demonstrate for the first time that KIN-A and KIN-B display a dynamic localisation pattern similar to other components of the CPC. Most of these data provide convincing evidence for KIN-A and KIN-B being bona fide CPC proteins, although the evidence that KIN-A and KIN-B translocate to the anterior end of the new FAZ at cytokinesis is weak - the KIN-A/B signals are very faint and difficult to see, and cell outlines/brightfield images are not presented to allow the reader to determine the cellular location of these faint signals (Fig S1B).

We thank the reviewer for their thorough assessment of our manuscript and the insightful feedback to further improve our study. To address the point above, we have acquired new microscopy data for Fig. S1B and S1C, which now includes phase contrast images, and have chosen representative cells in late anaphase and telophase. We hope that the signal of Aurora BAUK1, KIN-A and KIN-B at the anterior end of the new FAZ can be now distinguished more clearly.

They then demonstrate, by using RNAi to deplete individual components, that the CPC proteins have hierarchical interdependencies for their localisation to the kinetochores at metaphase. These experiments appear to have been well performed, although only images of cell nuclei were shown (Fig 2A), meaning that the reader cannot properly assess whether CPC components have localised elsewhere in the cell, or if their abundance changes in response to depletion of another CPC protein.

We chose to show close-ups of the nucleus to highlight the different localization patterns of CPC proteins under the different RNAi conditions. In none of these conditions did we observe mis-localization of CPC subunits to the cytoplasm. To clarify this point, we added the following sentence in the legend for Figure 2A:

‘A) Representative fluorescence micrographs showing the localization of YFP-tagged Aurora BAUK1, INCENPCPC1, KIN-A and KIN-B in 2K1N cells upon RNAi-mediated knockdown of indicated CPC subunits. Note that nuclear close-ups are shown here. CPC proteins were not detected in the cytoplasm. RNAi was induced with 1 μg/mL doxycycline for 24 h (KIN-B RNAi) or 16 h (all others). Cell lines: BAP3092, BAP2552, BAP2557, BAP3093, BAP2906, BAP2900, BAP2904, BAP3094, BAP2899, BAP2893, BAP2897, BAP3095, BAP3096, BAP2560, BAP2564, BAP3097. Scale bars, 2 μm.’

Ballmer and Akiyoshi then go on to determine the kinetochore localisation domains of KIN-A and KIN-B. Using ectopically expressed GFP-tagged truncations, they show that coiled-coil domains within KIN-A and KIN-B, as well as a disordered C-terminal tail present only in KIN-A, but not the N-terminal motor domains of KIN-A or KIN-B, are required for kinetochore localisation. These data are strengthened by immunoprecipitating CPC complexes and crosslinking them prior to mass spectrometry analysis (IP-CLMS), a state-of-the-art approach, to determine the contacts between the CPC components. Structural predictions of the CPC structure are also made using AlphaFold2, suggesting that coiled coils form between KIN-A and KIN-B, and that KIN-A/B interact with the N termini of CPC1 and CPC2. Experimental results show that CPC1 and CPC2 are unable to localise to kinetochores if they lack their N-terminal domains consistent with these predictions. Altogether these data provide convincing evidence of the protein domains required for CPC kinetochore localisation and CPC protein interactions. However, the authors also conclude that KIN-B plays a minor role in localising the CPC to kinetochores compared to KIN-A. This conclusion is not particularly compelling as it stems from the observation that ectopically expressed GFP-NLS-KIN-A (full length or coiled-coil domain + tail) is also present at kinetochores during anaphase unlike endogenously expressed YFP-KIN-A. Not only is this localisation probably an artifact of the ectopic expression, but the KIN-B coiled-coil domain localises to kinetochores from S to metaphase and Fig S2G appears to show a portion of the expressed KIN-B coiled-coil domain colocalising with KKT2 at anaphase. It is unclear why KIN-B has been discounted here.

As the reviewer points out, a small fraction of GFP-NLS-KIN-B317-624 is indeed detectable at kinetochores in anaphase, although most of the protein shows diffuse nuclear staining. There are various explanations for this phenomenon: It is conceivable that the KIN-B motor domain may contribute to microtubule binding and translocation of the CPC from kinetochores onto the spindle in anaphase. In our experiments, ectopically expressed KIN-B317-624 likely outcompetes a fraction of endogenous KIN-B for binding to KIN-A, which could interfere with this translocation process, leaving a population of CPC ‘stranded’ at kinetochores in anaphase. Another possibility, hinted at by the reviewer, is that the C-terminus of KIN-B interacts with receptors at the kinetochore/centromere. Although we do not discount this possibility, we nevertheless decided to focus on KIN-A in this study, because the anaphase kinetochore retention phenotype for both full-length GFP-NLS-KIN-A and -KIN-A309-862 is much stronger than for KIN-B317-624. Two additional reasons were that (i) KIN-A is highly conserved within kinetoplastids, whereas KIN-B orthologs are missing in some kinetoplastids, and (ii) no convincing interactions between KIN-B and kinetochore proteins were predicted by AF2.

To address the reviewer’s point, we decided to include KIN-B in the title of this manuscript, which now reads: ‘Dynamic localization of the chromosomal passenger complex is controlled by the orphan kinesins KIN-A and KIN-B in the kinetoplastid parasite Trypanosoma brucei’.

Moreover, we modified the corresponding paragraph in the results section as follows:

‘Intriguingly, unlike endogenously YFP-tagged KIN-A, ectopically expressed GFP fusions of both full-length KIN-A and KIN-A310-862 clearly localized at kinetochores even in anaphase (Figs. 2, F and H). Weak anaphase kinetochore signal was also detectable for KIN-B317-624 (Fig. S2F). GFP fusions of the central coiled-coil domain or the C-terminal disordered tail of KIN-A did not localize to kinetochores (data not shown). These results show that kinetochore localization of the CPC is mediated by KIN-A and KIN-B and requires both the central coiled-coil domain as well as the C-terminal disordered tail of KIN-A.’

Next, using a mixture of RNAi depletion and LacI-LacO recruitment experiments, the authors show that kinetochore proteins KKT7 and KKT9 are required for AUK1 to localise to kinetochores (other KKT8 complex components were not tested here) and that all components of the KKT8 complex are required for KIN-A kinetochore localisation. Further, both KKT7 and KKT8 were able to recruit AUK1 to an ectopic locus in the S phase, and KKT7 recruited KKT8 complex proteins, which the authors suggest indicates it is upstream of KKT8. However, while these experiments have been performed well, the reciprocal experiment to show that KKT8 complex proteins cannot recruit KKT7, which could have confirmed this hierarchy, does not appear to have been performed. Further, since the LacI fusion proteins used in these experiments were ectopically expressed, they were retained (artificially) at kinetochores into anaphase; KKT8 and KIN-A were both able to recruit AUK1 to LacO foci in anaphase, while KKT7 was not. The authors conclude that this suggests the KKT8 complex is the main kinetochore receptor of the CPC - while very plausible, this conclusion is based on a likely artifact of ectopic expression, and for that reason, should be interpreted with a degree of caution.

We previously showed that RNAi-mediated depletion of KKT7 disrupts kinetochore localization of KKT8 complex members, whereas kinetochore localization of KKT7 is unaffected by disruption of the KKT8 complex (Ishii and Akiyoshi, 2020). Moreover, in contrast to the KKT8 complex, KKT7 remains at kinetochores in anaphase (Akiyoshi and Gull, 2014). These data show that KKT7 is upstream of the KKT8 complex. In this context, the LacI-LacO tethering approach can be very useful to probe whether two proteins (or domains of proteins) could interact in vivo either directly or indirectly. However, a recruitment hierarchy cannot be inferred from such experiments because the data just shows whether X can recruit Y to an ectopic locus (but not whether X is upstream of Y or vice versa). Regarding the retention of Aurora BAUK1 at kinetochores in anaphase upon ectopic expression of GFP-KKT8-LacI, we agree with the reviewer that these data need to be carefully interpreted. Nevertheless, the notion that the KKT7-KKT8 complex recruits the CPC to kinetochores is also strongly supported by IP-MS, RNAi experiments, and AF2 predictions. For clarification and to address the reviewer’s point, we re-formulated the corresponding paragraph in the main text:

‘We previously showed that KKT7 lies upstream of the KKT8 complex (Ishii and Akiyoshi, 2020). Indeed, GFP-KKT72-261-LacI recruited tdTomato-KKT8, -KKT9 and -KKT12 (Fig. S4E). Expression of both GFP-KKT72-261-LacI and GFP-KKT8-LacI resulted in robust recruitment of tdTomato-Aurora BAUK1 to LacO foci in S phase (Figs. 4, E and F). Intriguingly, we also noticed that, unlike endogenous KKT8 (which is not present in anaphase), ectopically expressed GFP-KKT8-LacI remained at kinetochores during anaphase (Fig. 4F). This resulted in a fraction of tdTomato-Aurora BAUK1 being trapped at kinetochores during anaphase instead of migrating to the central spindle (Fig. 4F). We observed a comparable situation upon ectopic expression of GFP-KIN-A, which is retained on anaphase kinetochores together with tdTomato-KKT8 (Fig. S4F). In contrast, Aurora BAUK1 was not recruited to LacO foci marked by GFP- KKT72-261-LacI in anaphase (Fig. 4E).’

Further IP-CLMS experiments, in combination with recombinant protein pull-down assays and structural predictions, suggested that within the KKT8 complex, there are two subcomplexes of KKT8:KKT12 and KKT9:KKT11, and that KKT7 interacts with KKT9:KKT11 to recruit the remainder of the KKT8 complex. The authors also assess the interdependencies between KKT8 complex components for localisation and expression, showing that all four subunits are required for the assembly of a stable KKT8 complex and present AlphaFold2 structural modelling data to support the two subcomplex models. In general, these data are of high quality and convincing with a few exceptions. The recombinant pulldown assay (Fig. 4H) is not particularly convincing as the 3rd eluate gel appears to show a band at the size of KKT11 (despite the labelling indicating no KKT11 was present in the input) but no pulldown of KKT9, which was present in the input according to the figure legend (although this may be mislabeled since not consistent with the text). The text also states that 6HIS-KKT8 was insoluble in the absence of KKT12, but this is not possible to assess from the data presented.

We thank the reviewer for pointing out an error in the text: ‘Removal of both KKT9 and KKT11 did not impact formation of the KKT8:KKT12 subcomplex’ should read ‘Removal of either KKT9 or KKT11 did not impact formation of the KKT8:KKT12 subcomplex’. Regarding the very faint band perceived to be KKT11 in the 3rd eluate: This band runs slightly lower than KKT11 and likely represents a bacterial contaminant (which we have seen also in other preps in the past). We have made a note of this in the corresponding legend (new Fig. 4I). Moreover, we provide the estimated molecular weights for each subunit, as suggested by the reviewer in recommendation #14 (see below):

‘(I) Indicated combinations of 6HIS-tagged KKT8 (~46 kDa), KKT9 (~39 kDa), KKT11 (~29 kDa) and KKT12 (~23 kDa) were co-expressed in E. coli, followed by metal affinity chromatography and SDS-PAGE. The asterisk indicates a common contaminant.’

The corresponding paragraph in the results section now reads:

To validate these findings, we co-expressed combinations of 6HIS-KKT8, KKT9, KKT11 and KKT12 in E. coli and performed metal affinity chromatography (Fig. 4I). 6HIS-KKT8 efficiently pulled down KKT9, KKT11 and KKT12, as shown previously (Ishii and Akiyoshi, 2020). In the absence of KKT9, 6HIS-KKT8 still pulled down KKT11 and KKT12. Removal of either KKT9 or KKT11 did not impact formation of the KKT8:KKT12 subcomplex. In contrast, 6HIS-KKT8 could not be recovered without KKT12, indicating that KKT12 is required for formation of the full KKT8 complex. These results support the idea that the KKT8 complex consists of KKT8:KKT12 and KKT9:KKT11 subcomplexes.’

It is also surprising that data showing the effects of KKT8, KKT9, and KKT12 depletion on KKT11 localisation and abundance are not presented alongside the reciprocal experiments in Fig S4G-J.

YFP-KKT11 is delocalized upon depletion of KKT8 and KKT9 (see below). Unfortunately, we were unsuccessful in our attempts at deriving the corresponding KKT12 RNAi cell line, rendering this set of data incomplete. Because these data are not of critical importance for this study, we decided not to invest more time in attempting further transfections.

Author response image 1.

The authors also convincingly show that AlphaFold2 predictions of interactions between KKT9:KKT11 and a conserved domain (CD1) in the C-terminal tail of KIN-A are likely correct, with CD1 and a second conserved domain, CD2, identified through sequence analysis, acting synergistically to promote KIN-A kinetochore localisation at metaphase, but not being required for KIN-A to move to the central spindle at anaphase. They then hypothesise that the kinesin motor domain of KIN-A (but not KIN-B which is predicted to be inactive based on non-conservation of residues key for activity) determines its central spindle localisation at anaphase through binding to microtubules. In support of this hypothesis, the authors show that KIN-A, but not KIN-B can bind microtubules in vitro and in vivo. However, ectopically expressed GFP-NLS fusions of full-length KIN-A or KIN-A motor domain did not localise to the central spindle at anaphase. The authors suggest this is due to the GPF fusion disrupting the ATPase activity of the motor domain, but they provide no evidence that this is the case. Instead, they replace endogenous KIN-A with a predicted ATPase-defective mutant (G209A), showing that while this still localises to kinetochores, the kinetochores were frequently misaligned at metaphase, and that it no longer concentrates at the central spindle (with concomitant mis-localisation of AUK1), causing cells to accumulate at anaphase. From these data, the authors conclude that KIN-A ATPase activity is required for chromosome congression to the metaphase plate and its central spindle localisation at anaphase. While potentially very interesting, these data are incomplete in the absence of any experimental data to show that KIN-A possesses ATPase activity or that this activity is abrogated by the G209A mutation, and the conclusions of this section are rather speculative.

Thank you for this important comment, which relates to a similar point raised by Reviewer 1 (see above). Indeed, ATPase and motor activity of KIN-A remain to demonstrated biochemically using recombinant proteins, which is beyond the scope of this study. We generated MSAs of KIN-A and KIN-B from different kinetoplastids with human Kinesin-1, human Mklp2 and yeast Klp9, which are now presented in Figure 6A and S6A. These clearly show that key motifs required for ATP or tubulin binding in other kinesins are highly conserved in KIN-A (but not KIN-B). This includes the conserved glycine residue in the Switch II helix (G234 in human Kinesin-1, G210 in T. brucei KIN-A), which forms a hydrogen bond with the γ-phosphate of ATP, and upon mutation has been shown to impair ATPase activity and trap the motor head in a strong microtubule (‘rigor’) state (Rice et al., 1999; Sablin et al., 1996). The prominent rigor phenotype of KIN-AG210A is consistent with KIN-A having ATPase activity. In addition to the data in Fig. 6A and S6A, we made following changes to the main text:

‘We therefore speculated that anaphase translocation of the kinetoplastid CPC to the central spindle may involve the kinesin motor domain of KIN-A. KIN-B is unlikely to be a functional kinesin based on the absence of several well-conserved residues and motifs within the motor domain, which are fully present in KIN-A (Li et al., 2008). These include the P-loop, switch I and switch II motifs, which form the nucleotide binding cleft, and many conserved residues within the α4-L12 elements, which interact with tubulin (Fig. S6A) (Endow et al., 2010). Consistent with this, the motor domain of KIN-B, contrary to KIN-A, failed to localize to the mitotic spindle when expressed ectopically (Fig. S2E) and did not co-sediment with microtubules in our in vitro assay (Fig. S6B).

Ectopically expressed GFP-KIN-A and -KIN-A2-309 partially localized to the mitotic spindle but failed to concentrate at the midzone during anaphase (Figs. 2, F and G), suggesting that N-terminal tagging of the KIN-A motor domain may interfere with its function. To address whether the ATPase activity of KIN-A is required for central spindle localization of the CPC, we replaced one allele of KIN-A with a C-terminally YFP-tagged G210A ATP hydrolysis-defective rigor mutant (Fig. 6A) (Rice et al., 1999) and used an RNAi construct directed against the 3’UTR of KIN-A to deplete the untagged allele. The rigor mutation did not affect recruitment of KIN-A to kinetochores (Figs. S6, C and D). However, KIN-AG210A-YFP marked kinetochores were misaligned in ~50% of cells arrested in metaphase, suggesting that ATPase activity of KIN-A promotes chromosome congression to the metaphase plate (Figs. S6, E-H).’

Impact:

Overall, this work uses a wide range of cutting-edge molecular and structural predictive tools to provide a significant amount of new and detailed molecular data that shed light on the composition of the unusual trypanosome CPC and how it is assembled and targeted to different cellular locations during cell division. Given the fundamental nature of this research, it will be of interest to many parasitology researchers as well as cell biologists more generally, especially those working on aspects of mitosis and cell division, and those interested in the evolution of the CPC.

We thank the reviewer for his/her feedback and thoughtful and thorough assessment of our study.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Why did the authors omit KIN-B from the title?

We decided to add KIN-B in the title. Please see our response to Reviewer #3 (public review).

(2) Abstract, line 28, "Furthermore, the kinesin motor activity of KIN-A promotes chromosome alignment in prometaphase and CPC translocation to the central spindle upon anaphase onset." This must be revised - see public review.

We changed this section of the abstract as follows:

‘Furthermore, the ATPase activity of KIN-A promotes chromosome alignment in prometaphase and CPC translocation to the central spindle upon anaphase onset. Thus, KIN-A constitutes a unique ‘two-in-one’ CPC localization module in complex with KIN-B, which directs the CPC to kinetochores (from S phase until metaphase) via its C-terminal tail, and to the central spindle (in anaphase) via its N-terminal kinesin motor domain.’

(3) Line 87-90. The findings by Li et al., 2008 (KIN-A and KIN-B interacting with Aurora B and epistasis analysis) should be introduced more comprehensively in the Introduction section.

We added the following sentence in the introduction:

‘In addition, two orphan kinesins, KIN-A and KIN-B, have been proposed to transiently associate with Aurora BAUK1 during mitosis (Li et al., 2008; Li, 2012).’

(4) Figure 1B. The way the Trypanosoma cell cycle is defined should be briefly explained in the main text, rather than just referring to the figure.

The ‘KN’ annotation of the trypanosome cell cycle is explained in the Figure 1 legend. We now also added a brief description in the main text:

‘We next assessed the localization dynamics of fluorescently tagged KIN-A and KIN-B over the course of the cell cycle (Figs. 1, B-E). T. brucei possesses two DNA-containing organelles, the nucleus (‘N’) and the kinetoplast (‘K’). The kinetoplast is an organelle found uniquely in kinetoplastids, which contains the mitochondrial DNA and replicates and segregates prior to nuclear division. The ‘KN’ configuration serves as a good cell cycle marker (Woodward and Gull, 1990; Siegel et al., 2008).’

(5) Line 118. Throughout the paper, it is not clear why GFP-NLS fusion was used instead of GFP fusion. Please justify the fusion of NLS.

NLS refers to a short ‘nuclear localization signal’ (TGRGHKRSREQ) (Marchetti et al., 2000), which ensures that the ectopically expressed construct is imported into the nucleus. When we previously expressed truncations of KKT2 and KKT3 kinetochore proteins, many fragments did not go into the nucleus presumably due to the lack of an NLS, which prevented us from determining which domains are responsible for their kinetochore localization. We have since then consistently used this short NLS sequence in our inducible GFP fusions in the past without any complications. We added a sentence in the Materials & Methods section under Trypanosome culture: ‘All constructs for ectopic expression of GFP fusion proteins include a short nuclear localization signal (NLS) (Marchetti et al., 2000).’ To avoid unnecessary confusion, we removed ‘NLS’ from the main text and figures.

(6) Line 121, "Unexpectedly". It is not clear why this was unexpected.

To clarify this point, we modified this paragraph in the results section:

‘To our surprise, KIN-A-YFP and GFP-KIN-B exhibited a CPC-like localization pattern identical to that of Aurora BAUK1: Both kinesins localized to kinetochores from S phase to metaphase, and then translocated to the central spindle in anaphase (Figs. 1, C-E). Moreover, like Aurora BAUK1, a population of KIN-A and KIN-B localized at the new FAZ tip from late anaphase onwards (Figs. S1, B and C). This was unexpected, because KIN-A and KIN-B were previously reported to localize to the spindle but not to kinetochores or the new FAZ tip (Li et al., 2008). These data suggest that KIN-A and KIN-B are bona fide CPC proteins in trypanosomes, associating with AuroraAUK1, INCENPCPC1 and CPC2 throughout the cell cycle.’

(7) Line 127-129. Defining homologs and orthologs is tricky - there are many homologs and paralogs of kinesin-like proteins. The method to define the presence or absence of KIN-A/KIN-B homologs should be described in the Materials and Methods section.

Due to the difficulty in defining true orthologs for kinesin-like proteins, we took a conservative approach: reciprocal best BLAST hits. We first searched KIN-A homologs using BLAST in the TriTryp database or using hmmsearch using manually prepared hmm profiles. When the top hit in a given organism found T. brucei KIN-A in a reciprocal BLAST search in T. brucei proteome, we considered the hit as a true ortholog. We modified the Materials and Methods section as below.

‘Searches for homologous proteins were done using BLAST in the TriTryp database (Aslett et al., 2010) or using hmmsearch using manually prepared hmm profiles (HMMER version 3.0; Eddy, 1998). The top hit was considered as a true ortholog only if the reciprocal BLAST search returned the query protein in T. brucei.’

(8) Line 156. For non-experts of Trypanosoma cell biology, it is not clear how the nucleolar localization is defined.

The nucleolus in T. brucei is discernible as a DAPI-dim region in the nucleus.

(9) Fig.2G and Fig.S2F. These data imply that the coiled-coil and C-terminal tail domains of KIN-A/KIN-B are important for anaphase spindle midzone enrichment. However, it is odd that this was not mentioned. This reviewer recommends that the authors quantify the midzone localization data of these constructs and discuss the role of the coiled-coil domains.

One possibility is that KIN-A and KIN-B need to form a complex (via their coiled-coil domains) to localize to the spindle midzone. Another likely possibility, which is discussed in the manuscript, is that N-terminal tagging of KIN-A impairs motor activity. This is supported by the fact that the central spindle localization is also disrupted in full-length GFP-KIN-A. We decided not to provide a quantification for these data due to low sample sizes for some of the constructs (e.g. expression not observed in all cells).

(10) Line 288-289, "pLDDT scores improved significantly for KIN-A CD1 in complex with KKT9:KKT11 (>80) compared to KIN-A CD1 alone (~20) (Figs. S3, A and B)." I can see that pLDDT score is about 20 at KIN-A CD1 from Figs S3A, but the basis of pLDDT > 80 upon inclusion go KKT9:KKT11 is missing.

We added the pLDDT and PAE plots for the AF2 prediction of KIN-A700-800 in complex with KKT9:KKT11 in Fig. S5B.

(11) Fig. 5A. Since there is no supporting biochemical data for KIN-A-KKT9-KKT11 interaction, it is important to assess the stability of AlphaFold-based structural predictions of the KIN-A-KKT9-KKT11 interaction. Are there significant differences among the top 5 prediction results, and do these interactions remain stable after the "simulated annealing" process used in the AlphaFold predictions? Are predicted CD1-interacting regions/amino residues in KKT9 and KKT11 evolutionarily conserved?

See above. The interaction was predicted in all 5 predictions as shown in Fig. S5B. Conservation of the CD1-interacting regions in KKT9 and KKT11 are shown below:

Author response image 2.

KKT9 (residues ~53 – 80 predicted to interact with KIN-A in T. brucei)

Author response image 3.

KKT11 (residues 61-85 predicted to interact with KIN-A in T. brucei)

(12) Line 300, Fig. S5D and E, "failed to localize at kinetochores". From this resolution of the microscopy images, it is not clear if these proteins fail to localize at kinetochores as the KKT and KIN-A310-716 signals overlap. Perhaps, "failed to enrich at kinetochores" is a more appropriate statement.

We changed this sentence according to the reviewer’s suggestion.

(13) Line 309 and Fig 5D and F, "predominantly localized to the mitotic spindle". From this image shown in Fig 5D, it is not clear if KIN-A∆CD1-YFP and Aurora B are predominantly localized to the spindle or if they are still localized to centromeres that are misaligned on the spindle. Without microtubule staining, it is also not clear how microtubules are distributed in these cells. Please clarify how the presence or absence of kinetochore/spindle localization was defined.

As shown in Fig. S5E and S5F, deletion of CD1 clearly impairs kinetochore localization of KIN-A (kinetochores marked by tdTomato-KKT2). Moreover, misalignment of kinetochores, as observed upon expression of the KIN-AG210A rigor mutant, would result in an increase in 2K1N cells and proliferation defects, which is not the case for the KIN-A∆CD1 mutant (Fig. 5H, Fig. S5I). KIN-A∆CD1-YFP appears to localize diffusely along the entire length of the mitotic spindle, whereas we still observe kinetochore-like foci in the rigor mutant. Unfortunately, we do not have suitable antibodies that would allow us to distinguish spindle microtubules from the vast subpellicular microtubule array present in T. brucei and hence need to rely on tagging spindle-associated proteins such as MAP103.

(14) Fig. 5F, G, S5F. Along the same lines, it would be helpful to show example images for each category - "kinetochores", "kinetochores + spindle", and "spindle".

As suggested by the reviewer, we have now included example images for each category (‘kinetochores’, ‘kinetochores + spindle’, ‘spindle’) along with a schematic illustration in Fig. 5F.

(15) Line 332 and Fig. S6A. The experiment may be repeated in the presence of ATP or nonhydrolyzable ATP analogs.

We thank the reviewer for the suggestion. We envisage such experiments for an in-depth follow-up study.

(16) Line 342, "motor activity of KIN-A". Until KIN-A is shown to have motor activity, the result based on the rigor mutant does not show that the motor activity of KIN-A promotes chromosome congression. The result suggests that the ATPase activity of KIN-A is important.

We changed that sentence as suggested by the reviewer.

(17) Line 419 -. The authors base their discussion on the speculation that KIN-A is a plus-end directed motor. Please justify this speculation.

Indeed, the notion that KIN-A is a plus-end directed motor remains a hypothesis, which is based on sequence alignments with other plus-end directed motors and the observation that the KIN-A motor domain is involved in translocation of the CPC to the central spindle in anaphase. We have modified the corresponding section in the discussion as follows:

‘It remains to be investigated whether KIN-A truly functions as a plus-end directed motor. The role of the KIN-B in this context is equally unclear. Since KIN-B does not possess a functional kinesin motor domain, we deem it unlikely that the KIN-A:KIN-B heterodimer moves hand-over-hand along microtubules as do conventional (kinesin-1 family) kinesins. Rather, the KIN-A motor domain may function as a single-headed unit and drive processive plus-end directed motion using a mechanism similar to the kinesin-3 family kinesin KIF1A (Okada and Hirokawa, 1999).’

(18) Line 422-423, "plus-end directed motion using a mechanism similar to kinesin-3 family kinesins (such as KIF1A)." Please cite a reference supporting this statement.

See above. We cited a paper by (Okada and Hirokawa, 1999).

Reviewer #2 (Recommendations For The Authors):

Please provide a quantification of data shown in Figure 2F-H and described in lines 151-166.

We decided not to provide a quantification for these data due to low sample sizes for some of the constructs (e.g. expression not observed in all cells).

It appears as if the paper more or less follows a chronological order of the experiments that were performed before AF multimer enabled the insightful and compelling structural analysis. That is a matter of style, but in some cases, the writing could be updated, shortened, or re-arranged into a more logical order. Concrete examples:

(i) Line 144: "we did not include CPC2 for further analysis in this study" Although CPC2 features at a prominent and interesting position in the predicted structures of the kinetoplastid CPC, shown in later main figures.

We attempted RNAi-mediated depletion of CPC2 using two different shRNA constructs. However, we cannot exclude the possibility that the knockdown of CPC2 was less efficient compared with the other CPC subunits. For this reason, we decided to remove all the data on CPC2 from Fig. S2.

(ii) The work with the KIN-A motor domain only and KIN-A ∆motor domain (Fig 2) begs the question about a more subtle mutation to interfere with the motor domain. Which is ultimately presented in Fig 6. I think that the final paragraph and Figure 6 follow naturally after Figure 2.

We appreciate the suggestion. However, we would like to keep Figure 6 there.

(iii) The high-confidence structural predictions in Fig 3 and Fig 4 are insightful. The XL-MS descriptions that precede them are not so helpful (Fig 3A and 4G and in the text). To emphasize their status as experimental support for the predicted structures, which is very important, it would be good to discuss the XL-MS after presenting the models.

As suggested, we have re-arranged the text and/or figures such that the AF2 predictions are discussed first and the CLMS data are brought in afterwards.

Figure 1A prominently features an arbitrary color code and a lot of protein IDs without a legend. That is not a very convincing start. Figure S1 is more informative, containing annotated protein names and results of the KIN-A and KIN-B IPs. Please improve Figure 1A, for example by presenting a modified version of Figure S1. In all these types of figures, please list both protein names and gene IDs.

We agree with the reviewer that the IP-MS data in Fig. S1 is more informative and hence decided to swap the heatmaps in Fig. 1A and Fig. S1A. We further annotated the heatmap corresponding to the Aurora BAUK1 IP-MS (now presented in Fig. S1) as suggested by the reviewer.

The visualization of the structural predictions is not consistent among figures:

(i) The structure in Fig 4I is important and could be displayed larger. The pLDDT scores, and especially those of the non-displayed models, do not add much information and should not be a main panel. If the authors want to display the pLDDT scores, I recommend a panel (main or supplement) of the structure colored for local prediction confidences, as in Fig 5A.

(ii) In Figure 5A itself, it is hard to follow the chains in general, and KIN-A in particular, since the structure is pLDDT-coloured. Please present an additional panel colored by chain (consistent with Fig 4I, as mentioned above).

(iii) The summarizing diagram, currently displayed as Fig 4J, should be placed after Fig 5A and take the discovered KIN-A - KKT9-11 connection into account. Ideally, it also covers the suspected importance of the motor domain and serves as a summarising diagram.

We thank the reviewer for the constructive comments. For each structure prediction, we now present two images side by side; one coloured by chain and one colored by pLDDT. We recently re-ran AF2 for the full CPC and also for the KKT7N-KKT8 complex, and got improved predictions. Hence some of the models in Fig. 3/S3 and Fig. 4/S4 have been updated accordingly. For the CLMS plots, we also decided to colour the cross-links according to whether the 30 angstrom distance constraints were fulfilled or not in the AF2 prediction. We also increased the size of the structures shown in Fig. 4. Furthermore, we decided to remove the summarizing diagram from Fig. 4 and instead made a new main Fig. 7, which shows a more detailed schematic, which also takes into account the proposed function of the KIN-A motor domain, as suggested by the reviewer, and other points addressed in the Discussion.

The methods section for the structural predictions lacks essential information. Predictions can only be reproduced if the version of AF2 multimer v2.x is specified and key parameters are mentioned.

As suggested, we have added the details in the Materials and Methods section as follows.

‘Structural predictions of KIN-A/KIN-B, KIN-A310-862/KIN-B317-624, CPC1/CPC2/KIN-A300-599/KIN-B 317-624, and KIN-A700-800/KKT9/KKT11 were performed using ColabFold version 1.3.0 (AlphaFold-Multimer version 2), while those of AUK1/CPC1/CPC2/KIN-A1-599/KIN-B, KKT71-261/KKT9/KKT11/KKT8/KKT12, KKT9/KKT11/KKT8/KKT12, and KKT71-261/KKT9/KKT11 were performed using ColabFold version 1.5.3 (AlphaFold-Multimer version 2.3.1) using default settings, accessed via https://colab.research.google.com/github/sokrypton/ColabFold/blob/v1.3.0/AlphaFold2.ipynb and https://colab.research.google.com/github/sokrypton/ColabFold/blob/v1.5.3/AlphaFold2.ipynb.’

Line 121, please explain the "Unexpectedly" by including a reference to the work from Li and colleagues. A statement with some details would be useful, as the difference between both studies appears to be crucial for the novelty of this paper. Alternatively, refer to this being covered in the discussion.

To clarify this point, we modified this paragraph in the results section:

‘To our surprise, KIN-A-YFP and GFP-KIN-B exhibited a CPC-like localization pattern identical to that of Aurora BAUK1: Both kinesins localized to kinetochores from S phase to metaphase, and then translocated to the central spindle in anaphase (Figs. 1, C-E). Moreover, like Aurora BAUK1, a population of KIN-A and KIN-B localized at the new FAZ tip from late anaphase onwards (Figs. S1, B and C). This was unexpected, because KIN-A and KIN-B were previously reported to localize to the spindle but not to kinetochores or the new FAZ tip (Li et al., 2008). These data suggest that KIN-A and KIN-B are bona fide CPC proteins in trypanosomes, associating with AuroraAUK1, INCENPCPC1 and CPC2 throughout the cell cycle.’

Line 285 refers to "conserved" regions in the C-terminal part of KIN-A, referring to Figure 5. Please expand the MSA in Figure 5B to get an idea about the conservation/variation outside CD1 and CD2.

We now present the full MSA for KIN-A proteins in kinetoplastids in Fig. S5A.

Please specify what is meant by Line 367-369 for someone who is not familiar with the work by Komaki et al. 2022. Either clarify in the text or clarify in the text with data to support it.

We updated the corresponding section in the discussion as follows:

‘Komaki et al. recently identified two functionally redundant CPC proteins in Arabidopsis, Borealin Related Interactor 1 and 2 (BORI1 and 2), which engage in a triple helix bundle with INCENP and Borealin using a conserved helical domain but employ an FHA domain instead of a BIR domain to read H3T3ph (Komaki et al., 2022).’

Data presented in Figure S6A, the microtubule co-sedimentation assay, is not convincing since a substantial amount of KIN-A/B is pelleted in the absence of microtubules. Did the authors spin the proteins in BRB80 before the assay to continue with soluble material and reduce sedimentation in the absence of microtubules? If the authors want to keep the wording in lines 331-332, the MT-binding properties of KIN-A and KIN-B need to be investigated in more detail, for example with a titration and a quantification thereof. Otherwise, they should change the text and replace "confirms" with "is consistent with". In any case, the legend needs to be expanded to include more information.

To address the point above, we have added the following text in the legend corresponding to Fig. S6:

‘Microtubule co-sedimentation assay with 6HIS-KIN-A2-309 (left) and 6HIS-KIN-B2-316 (right). S and P correspond to supernatant and pellet fractions, respectively. Note that both constructs to some extent sedimented even in the absence of microtubules. Hence, lack of microtubule binding for KIN-B may be due to the unstable non-functional protein used in this study.’

We have also updated the main text in the results section:

‘We therefore speculated that anaphase translocation of the kinetoplastid CPC to the central spindle may involve the kinesin motor domain of KIN-A. KIN-B is unlikely to be a functional kinesin based on the absence of several well-conserved residues and motifs within the motor domain, which are fully present in KIN-A (Li et al., 2008). These include the P-loop, switch I and switch II motifs, which form the nucleotide binding cleft, and many conserved residues within the α4-L12 elements, which interact with tubulin (Fig. S6A) (Endow et al., 2010). Consistent with this, the motor domain of KIN-B, contrary to KIN-A, failed to localize to the mitotic spindle when expressed ectopically (Fig. S2E) and did not co-sediment with microtubules in our in vitro assay (Fig. S6B).’

Details:

The readability of the pAE plots could be improved by arranging sequences according to their position in the structure. For example in Fig4I, KKT8 could precede KKT12. If it is easy to update this, the authors might want to do so.

We re-ran the AF2 predictions for the KKT7N – KKT8 complex in Fig. 4/S4 and changed the order according to the reviewer’s suggestion (KKT9:KKT11:KKT8:KKT12).

The same paper is referred to as Je Van Hooff et al. 2017 and as Van Hooff et al. 2017

Thank you for pointing this out. We have corrected the citation.

Reviewer #3 (Recommendations For The Authors):

(1) Please state at the end of the introduction/start of the results section that this work was performed in procyclic trypanosomes. Given that the cell cycles of procyclic and bloodstream forms differ, this is important.

We added this information at the end of the introduction:

‘Here, by combining biochemical, structural and cell biological approaches in procyclic form T. brucei, we show that the trypanosome CPC is a pentameric complex comprising Aurora BAUK1, INCENPCPC1, CPC2 and the two orphan kinesins KIN-A and KIN-B.’

(2) Please define NLS at first use (line 118), and for clarity, explain the rationale for using GFP with an NLS.

NLS refers to a short ‘nuclear localization signal’ (TGRGHKRSREQ) (Marchetti et al., 2000), which ensures that the ectopically expressed construct is imported into the nucleus. When we previously expressed truncations of KKT2 and KKT3 kinetochore proteins, many fragments did not go into the nucleus presumably due to the lack of an NLS, which prevented us from determining which domains are responsible for their kinetochore localization. We have since then consistently used this short NLS sequence in our inducible GFP fusions in the past without any complications. We added a sentence in the Materials & Methods section under Trypanosome culture: ‘All constructs for ectopic expression of GFP fusion proteins include a short nuclear localization signal (NLS) (Marchetti et al., 2000).’ To avoid unnecessary confusion, we removed ‘NLS’ from the main text and figures.

(3) Lines 148-150 - it would strengthen this claim if KIN-A/B protein levels were assessed by Western blot.

We now present a Western blot in Fig. S2C, showing that bulk KIN-B levels are clearly reduced upon KIN-A RNAi. The same is true also to some extent for KIN-A levels upon KIN-B RNAi, although this is less obvious, possibly due to the lower efficiency of KIN-B compared to KIN-A RNAi as judged by fluorescence microscopy (quantified in Fig. 2D and 2E).

(4) Line 253 - the text mentions the removal of both KKT9 and KKT11, which is not consistent with the figure (Fig 4H) - do you mean the removal of either KKT9 or KKT11?

Yes, we thank the reviewer for pointing out this mistake in the text, which has now been corrected.

(5) Line 337 - please include a reference for the G209A ATPase-defective rigor mutant - has this been shown to result in KIN-A being inactive previously?

Please see above our answer in public review.

(6) It is not always obvious when fluorescent fusion proteins are being expressed endogenously or ectopically, or when they are being expressed in an RNAi background or not without tracing the cell lines in Table S1 - please ensure this is clearly stated throughout the manuscript.

We now made sure that this is clearly stated in the main text as well as in the figure legends.

(7) Line 410 - 'KIN-A C-terminal tail is stuffed full of conserved CDK1CRK3 sites' - what does 'stuffed full' really mean (this is rather imprecise) and what are the consensus sites - are these CDK1 consensus sites that are assumed to be conserved for CRK3? I'm not aware of consensus sites for CRK3 having been determined, but if they have, this should be referenced.

We have modified the corresponding section in the discussion as follows:

‘In support of this, the KIN-A C-terminal tail harbours many putative CRK3 sites (10 sites matching the minimal S/T-P consensus motif for CDKs) and is also heavily phosphorylated by Aurora BAUK1 in vitro (Ballmer et al. 2024). Finally, we speculate that the interaction of KIN-A motor domain with microtubules, coupled to the force generating ATP hydrolysis and possibly plus-end directed motion, eventually outcompetes the weakened interactions of the CPC with the kinetochore and facilitates the extraction of the CPC from chromosomes onto spindle microtubules during anaphase. Indeed, deletion of the KIN-A motor domain or impairment of its motor function through N-terminal GFP tagging causes the CPC to be trapped at kinetochores in anaphase. Central spindle localization is additionally dependent on the ATPase activity of the KIN-A motor domain as illustrated by the KIN-A rigor mutant.’

(8) Lines 412-416: this proposal is written rather definitively - given no motor activity has been demonstrated for KIN-A, please make clear that this is still just a theory.

See above.

(9) Fig 1: KKT2 is not highlighted in Fig 1A - given this has been used for colocalization in Fig 1C-E, was it recovered, and if not, why not? Fig 1B-E: the S phase/1K1N terminology is somewhat misleading. Not all S phase cells will have elongated kinetoplasts - usually an asterisk is used to signify replicated DNA, not kinetoplast shape. If it is to be used here for elongation, then for consistency, N should be used for G2/mitotic cells.

Fig. 1A (now Fig. S1A) only shows the tip 30 hits. KKT2 was indeed recovered with Aurora BAUK1 (see Table S2) and is often used as a kinetochore marker in trypanosomes by our lab and others since the signal of fluorescently tagged KKT2 is relatively bright and KKT2 localizes to centromeres throughout the cell cycle.

(10) A general comment for all image figures is that these do not have accompanying brightfield images and it is therefore difficult to know where the cell body is, or sometimes which nuclei and kinetoplasts belong to which cell where DNA from more than one cell is within the image. It would be beneficial if brightfield images could be added, or alternatively, the cell outlines were traced onto DAPI or merged images. Also, brightfield images would allow the stage of cytokinesis (pre-furrowing/furrowing/abscission) in anaphase cells to be determined.

Since this study primarily addresses the recruitment mechanism of the CPC to kinetochores and to the central spindle from S phase to metaphase and in anaphase, respectively, and CPC proteins are not observed outside of the nucleus during these cell cycle stages, we did not present brightfield images in the figures. However, this point is particularly valid for discerning the localization of KIN-A and KIN-B to the new FAZ tip from late anaphase onwards. Hence, we acquired new microscopy data for Fig. S1B and S1C, which now includes phase contrast images, and have chosen representative cells in late anaphase and telophase. We hope that the signal of Aurora BAUK1, KIN-A and KIN-B at the anterior end of the new FAZ can be now distinguished more clearly.

(11) Fig 2A: legend should state that the micrographs show the localisation of the proteins within the nucleus as whole cells are not shown. 2C: can INCENP not be split into 2 lines - the 'IN' looks like 1N at first glance, which is confusing.

We have applied the suggested change in Fig. 2.

(12) Fig 3 (and other AF2 figures): Could the lines for satisfied & not satisfied in the key be thicker so they more closely resemble the lines in the figure and are less likely to be confused with the disordered regions of the CPC components?

We have now made those lines thicker.

(13) Why were different E value thresholds used in Fig 3 and Fig 4?

The CLMS data in Fig. 3 and Fig. 4 now both use the same E value threshold of E-3 (previously E-4 was used in Fig. 4). To determine a sensible significance threshold, we included some yeast protein sequences (‘false positives’) in the database used in pLink2 for identification of crosslinked peptides. Note that we recently also re-ran AF2 for the full CPC and for the KKT7N-KKT8 complex and got improved predictions. Hence some of the models in Fig. 3/S3 and Fig. 4/S4 have been updated accordingly. For the CLMS plots, we also decided to colour the cross-links according to whether the 30 angstrom distance constraints were fulfilled or not in the AF2 prediction.

(14) Fig 4H legend - please give the expected sizes of these recombinant proteins & check the 3rd elution panel (see public review comments).

See above response in public review.

(15) Fig 4I - please explain what the colours of the PAE plot and the values in the key signify, as well as how the Scored Residue values are arrived at. Please also define the pIDDT in the legend.

We have cited DeepMind’s 2021 methods paper, in which the outputs of AlphaFold are explained in detail. We also added a short description of the pLDDT and PAE scores and the corresponding colour coding in the legends of Fig. 3 and Fig. 4, respectively.

From figure 3 legend:

‘(B) Cartoon representation showing two orientations of the trypanosome CPC, coloured by protein on the left (Aurora BAUK1: crimson, INCENPCPC1: green, CPC2: cyan, KIN-A: magenta, and KIN-B: yellow) or according to their pLDDT values on the right, assembled from AlphaFold2 predictions shown in Figure S3. The pLDDT score is a per-residue estimate of the confidence in the AlphaFold prediction on a scale from 0 – 100. pLDDT > 70 (blue, cyan) indicates a reasonable accuracy of the model, while pLDDT < 50 (red) indicates a low accuracy and often reflects disordered regions of the protein (Jumper et al., 2021). BS3 crosslinks in (B) were mapped onto the model using PyXlinkViewer (blue = distance constraints satisfied, red = distance constraints violated, Cα-Cα Euclidean distance threshold = 30 Å) (Schiffrin et al., 2020).’

From Figure 4 legend:

‘(G) AlphaFold2 model of the KKT7 – KKT8 complex, coloured by protein (KKT71-261: green, KKT8: blue, KKT12: pink, KKT9: cyan and KKT11: orange) (left) and by pLDDT (center). BS3 crosslinks in (H) were mapped onto the model using PyXlinkViewer (Schiffrin et al., 2020) (blue = distance constraints satisfied, red = distance constraints violated, Cα-Cα Euclidean distance threshold = 30 Å). Right: Predicted Aligned Error (PAE) plot of model shown on the left (rank_2). The colour indicates AlphaFold’s expected position error (blue = low, red = high) at the residue on the x axis if the predicted and true structures were aligned on the residue on the y axis (Jumper et al., 2021).’

(16) Fig 6 legend - Line 730 should say (F) not (C).

Thank you for pointing out this typo.

(17) Fig S1A - a key is missing for the colours. Fig S1B/C - cell outlines or a brightfield image are really needed here - see earlier comment. Fig S1D - there doesn't seem to be a method for how this tree was generated.

See above response in public review regarding Fig. S1A and S1B/C. The tree in Fig. S1D is based on (Butenko et al., 2020).

(18) Fig S2: A: how was protein knockdown validated (especially for CPC2 where there was little obvious phenotype)? Fig S2B: the y-axis should read proportion of cells, not percentage. Fig S2E - NLS should be labelled.

Thank you for pointing out the mistake in the labelling.

(19) Fig S3: PAE plots should be labelled with protein names, not A-E. Similarly, the pIDDT plots should be labelled as in Fig 4I.

We have corrected the labelling in Fig. S3.

(20) Fig S5A-D - cell cycle stage labels are missing from images.

Thank you for pointing out the missing cell cycle stage labels.

Addition by editor:

In line 126 the statement that KIN-A and KIN-B "associate with Aurora-AUK1, INCENP-CPC1 and CPC2 throughout the cell cycle" seems too strong. There is no direct evidence for this. Please re-phrase as "likely associate" or "suggest... that ... may...".

We have modified that sentence according to the editor’s suggestion.

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Reviewer #1 (Public Review):

Summary:

The CPC plays multiple essential roles in mitosis such as kinetochore-microtubule attachment regulation, kinetochore assembly, spindle assembly checkpoint activation, anaphase spindle stabilization, cytokinesis, and nuclear envelope formation, as it dynamically changes its mitotic localization: it is enriched at inner centromeres from prophase to metaphase but it is relocalized at the spindle midzone in anaphase. The business end of the CPC is Aurora B and its allosteric activation module IN-box, which is located at the C-terminus of INCENP. In most well-studied eukaryotic species, Aurora B activity is locally controlled by the localization module of the CPC, Survivin, Borealin and the N-terminal portion of INCENP. Survivin and Borealin, which bind the N-terminus of INCENP, recognize histone residues that are specifically phosphorylated in mitosis, while anaphase spindle midzone localization is supported by the direct microtubule-binding capacity of the SAH (single alpha helix) domain of INCENP and other microtubule-binding proteins that specifically interact with INCENP during anaphase, which are under the regulation of CDK activity. One of these examples includes the kinesin-like protein MKLP2 in vertebrates. Trypanosoma is an evolutionarily interesting species to study mitosis since its kinetochore and centromere proteins do not show any similarity to other major branches of eukaryotes, while orthologs of Aurora B and INCENP have been identified. Combining molecular genetics, imaging, biochemistry, cross-linking IP-MS (IP-CLMS), and structural modeling, this manuscript reveals that two orphan kinesin-like proteins KIN-A and KIN-B act as localization modules of the CPC in Trypanosoma brucei. The IP-CLMS, AlphaFold2 structural predictions, and domain deletion analysis support the idea that (1) KIN-A and KIN-B form a heterodimer via their coiled-coil domains, (2) Two alpha helices of INCENP interact with the coiled-coil of the KIN-A-KIN-B heterodimer, (3) conserved KIN-A C-terminal CD1 and CD2 interact with the heterodimeric KKT9-KKT11 complex, which is a submodule of the KKT7-KKT8 kinetochore complex composed of KKT7, KKT8, KKT9, KKT11, and KKT12 unique to Trypanosoma, (4) KIN-A and KIN-B coiled-coil domains and the KKT7-KKT8 complex are required for CPC localization at the centromere, (5) CD1 and CD2 domains of KIN-A support its centromere localization. The authors further introduced a KIN-A rigor mutant and knocked-down wild-type KIN-A to show that the ATPase activity of KIN-A seems dispensable for centromere targeting but critical for spindle midzone enrichment of the CPC. The imaging data of the KIN-A rigor mutant suggest that dynamic KIN-A-microtubule interaction is required for metaphase alignment of the kinetochores and proliferation. Overall, the study reveals novel pathways of CPC localization regulation via KIN-A and KIN-B by multiple complementary approaches.

Strengths:

The major conclusion is collectively supported by multiple approaches, combining CRISPR-mediated gene deletion and complementation/site specific genome engineering, epistasis analysis of cellular localization, AlphaFold2 structure prediction of protein complexes, IP-CLMS and biochemical reconstitution (the complex of KKT8, KKT9, KKT11 and KKT12)

Weaknesses:

Minor weakness. The authors imply that KIN-A, but not KIN-B, interacts with microtubules based on microtubule pelleting assay (Fig. S6), but the substantial insoluble fractions of 6HIS-KINA and 6HIS-KIN-B make it difficult to conclusively interpret the data. It is possible that these two proteins are not stable unless they form a heterodimer.

Reviewer #2 (Public Review):

How the chromosomal passenger complex (CPC) and its subunit Aurora B kinase regulate kinetochore-microtubule attachment, and how the CPC relocates from kinetochores to the spindle midzone as a cell transitions from metaphase to anaphase are questions of great interest. In this study, Ballmer and Akiyoshi take a deep dive into the CPC in T. brucei, a kinetoplastid parasite with a kinetochore composition that varies greatly from other organisms.

Using a combination of approaches, most importantly in silico protein predictions using alphafold multimer and light microscopy in dividing T. brucei, the authors convincingly present and analyse the composition of the T. brucei CPC. This includes the identification of KIN-A and KIN-B, proteins of the kinesin family. This is a clear advancement over earlier work, for example by Li and colleagues in 2008. The involvement of KIN-A and KIN-B is of particular interest, as it provides a clue for the (re)localization of the CPC during the cell cycle. The evolutionary perspective makes the paper potentially interesting for a wide audience of cell biologists, a point that the authors bring across properly in the title, the abstract, and their discussion.

The evolutionary twist of the paper would be strengthened 'experimentally' by predictions of the structure of the CPC beyond T. brucei. Depending on how far the authors can extend their in-silico analysis, it would be of interest to discuss a) available/predicted CPC structures in well-studied organisms and b) structural predictions in other euglenozoa. What are the general structural properties of the CPC (e.g. flexible linkers, overall dimensions, structural differences when subunits are missing etc.)? How common is the involvement of kinesin-like proteins?

Reviewer #3 (Public Review):

Summary:

The protein kinase, Aurora B, is a critical regulator of mitosis and cytokinesis in eukaryotes, exhibiting a dynamic localisation. As part of the Chromosomal Passenger Complex (CPC), along with the Aurora B activator, INCENP, and the CPC localisation module comprised of Borealin and Survivin, Aurora B travels from the kinetochores at metaphase to the spindle midzone at anaphase, which ensures its substrates are phosphorylated in a time- and space-dependent manner. In the kinetoplastid parasite, T. brucei, the Aurora B orthologue (AUK1), along with an INCENP orthologue known as CPC1, and a kinetoplastid-specific protein CPC2, also displays a dynamic localisation, moving from the kinetochores at metaphase, to the spindle midzone at anaphase, to the anterior end of the newly synthesised flagellum attachment zone (FAZ) at cytokinesis. However, the trypanosome CPC lacks orthologues of Borealin and Survivin, and T. brucei kinetochores also have a unique composition, being comprised of dozens of kinetoplastid-specific proteins (KKTs). Of particular importance for this study are KKT7 and the KKT8 complex (comprising KKT8, KKT9, KKT11, and KKT12). Here, Ballmer and Akiyoshi seek to understand how the CPC assembles and is targeted to its different locations during the cell cycle in T. brucei.

Strengths & Weaknesses:

Using immunoprecipitation and mass-spectrometry approaches, Ballmer and Akiyoshi show that AUK1, CPC1, and CPC2 associate with two orphan kinesins, KIN-A and KIN-B, and with the use of endogenously expressed fluorescent fusion proteins, demonstrate for the first time that KIN-A and KIN-B display a dynamic localisation pattern similar to other components of the CPC, providing compelling evidence for KIN-A and KIN-B being bona fide CPC proteins.

They then demonstrate, by using RNAi to deplete individual components, that the CPC proteins have hierarchical interdependencies for their localisation to the kinetochores at metaphase. These experiments appear to have been well performed.

Ballmer and Akiyoshi then go on to determine the kinetochore localisation domains of KIN-A and KIN-B. Using ectopically expressed GFP-tagged truncations, they show that coiled coil domains within KIN-A and KIN-B, as well as a disordered C-terminal tail present only in KIN-A, but not the N-terminal motor domains of KIN-A or KIN-B, are required for kinetochore localisation. These data are strengthened by immunoprecipitating CPC complexes and crosslinking them prior to mass spectrometry analysis (IP-CLMS), a state-of-the-art approach, to determine the contacts between the CPC components. Structural predictions of the CPC structure are also made using AlphaFold2, suggesting that coiled coils form between KIN-A and KIN-B, and that KIN-A/B interact with the N termini of CPC1 and CPC2. Experimental results showing that CPC1 and CPC2 are unable to localise to kinetochores if they lack their N-terminal domains are consistent with these predictions. Altogether these data provide compelling evidence of the protein domains required for CPC kinetochore localisation and CPC protein interactions and indicate that both KIN-A and KIN-B have a role to play.

Next, using a mixture of RNAi depletion and LacI-LacO recruitment experiments, the authors show that kinetochore proteins KKT7 and KKT9 are required for AUK1 to localise to kinetochores (other KKT8 complex components were not tested here) and that all components of the KKT8 complex are required for KIN-A kinetochore localisation. Further, both KKT7 and KKT8 were able to recruit AUK1 to an ectopic locus in S phase, and KKT7 recruited KKT8 complex proteins, indicating it is upstream of KKT8, in line with previous work showing kinetochore localization of KKT7 is unaffected by disruption of the KKT8 complex. This leads to the conclusion that the KKT8 complex is likely the main kinetochore receptor of the CPC.

Further IP-CLMS experiments, in combination with recombinant protein pull down assays and structural predictions, suggested that within the KKT8 complex, there are two subcomplexes of KKT8:KKT12 and KKT9:KKT11, and that KKT7 interacts with KKT9:KKT11 to recruit the remainder of the KKT8 complex. The authors also assess the interdependencies between KKT8 complex components for localisation and expression, showing that all four subunits are required for the assembly of a stable KKT8 complex and present AlphaFold2 structural modelling data to support the two subcomplex model. In general, these data are of high quality and convincing, although it is a shame that data showing the effects of KKT8, KKT9 and KKT12 depletion on KKT11 localisation and abundance could not be presented alongside the reciprocal experiments in Fig S4I-L.

The authors also convincingly show that AlphaFold2 predictions of interactions between KKT9:KKT11 and a conserved domain (CD1) in the C-terminal tail of KIN-A are correct, with CD1 and a second conserved domain, CD2, identified through sequence analysis, acting synergistically to promote KIN-A kinetochore localisation at metaphase, but not being required for KIN-A to move to the central spindle at anaphase. They then hypothesise that the kinesin motor domain of KIN-A (but not KIN-B which is predicted to be inactive based on non-conservation of residues key for activity) determines its central spindle localisation at anaphase through binding to microtubules. In support of this hypothesis, the authors show that KIN-A, but not KIN-B can bind microtubules in vitro and in vivo. However, ectopically expressed GFP-NLS fusions of full length KIN-A or KIN-A motor domain did not localise to the central spindle at anaphase. The authors suggest this is due to the GFP fusion disrupting the ATPase activity of the motor domain, although they provide no evidence that this is the case. Instead, they replace endogenous KIN-A with a predicted ATPase-defective mutant (G210A), showing that while this still localises to kinetochores, the kinetochores were frequently misaligned at metaphase, and that it no longer concentrates at the central spindle (with concomitant mis-localisation of AUK1), causing cells to accumulate at anaphase. From these data, the authors conclude that KIN-A ATPase activity is required for chromosome congression to the metaphase plate and its central spindle localisation at anaphase. While these data are highly suggestive that KIN-A possesses ATPase activity, and that this activity is essential for its function, definitive biochemical evidence of KIN-A's ATPase activity is still lacking.

Impact:

Overall, this work uses a wide range of cutting edge molecular and structural predictive tools to provide a significant amount of new and detailed molecular data that shed light on the composition of the unusual trypanosome CPC and how it is assembled and targeted to different cellular locations during cell division. Given the fundamental nature of this research, it will be of interest to many parasitology researchers as well as cell biologists more generally, especially those working on aspects of mitosis and cell division, and those interested in the evolution of the CPC.

eLife assessment

This paper investigates how the EWS::FLI1 fusion protein organizes chromatin topology and regulates gene expression in an aggressive pediatric bone cancer known as Ewing sarcoma. The authors used the most recent genomics methodologies to provide a solid base of evidence for the role of a short alpha helix in the DNA binding domain of FLI1 in modulating binding to GGAA microsatellites and promoting enhancer activity. The study provides valuable insight into the underlying oncogenic mechanisms in Ewing sarcoma, but is limited to a single cell line and would benefit from consolidation of the main conclusions using additional techniques.

Reviewer #1 (Public Review):

Summary:

Ewing sarcoma is an aggressive pediatric cancer driven by the EWS-FLI oncogene. Ewing sarcoma cells are addicted to this chimeric transcription factor, which represents a strong therapeutic vulnerability. Unfortunately, targeting EWS-FLI has proven to be very difficult, and a better understanding of how this chimeric transcription factor works is critical to achieving this goal. Towards this perspective, the group had previously identified a DBD-𝛼4 helix (DBD) in FLI that appears to be necessary to mediate EWS-FLI transcriptomic activity. Here, the authors used multi-omic approaches, including CUT&tag, RNAseq, and MicroC to investigate the impact of this DBD domain. Importantly, these experiments were performed in the A673 Ewing sarcoma model where endogenous EWS-FLI was silenced, and EWS-FLI-DBD proficient or deficient isoforms were re-expressed (isogenic context). They found that the DBD domain is key to mediating EWS-FLI cis activity (at msat) and to generating the formation of specific TADs. Furthermore, cells expressing DBD-deficient EWS-FLI display very poor colony-forming capacity, highlighting that targeting this domain may lead to therapeutic perspectives.

Strengths:

The group has strong expertise in Ewing sarcoma genetics and epigenetics and also in using and analyzing this model (Theisen et al., 2019; Boone et al., 2021; Showpnil et al., 2022).

They aim at better understanding how EWS-FLI mediated its oncogenic activity, which is critical to eventually identifying novel therapies against this aggressive cancer.

They use the most recent state-of-the-art omics methods to investigate transcriptome, epigenetics, and genome conformation methods. In particular, Micro-C enables achieving up to 1kb resolved 3D chromatin structures, making it possible to investigate a large number of TADs and sub-TADs structures where EWS-FLI1 mediates its oncogenic activity.

They performed all their experiments in an Ewing sarcoma genetic background (A673 cells) which circumvents bias from previously reported approaches when working in non-orthologous cell models using similar approaches.

Weaknesses:

The main weakness comes from the poor reproducibility of Micro-C data. Indeed, it appears that the distances/clustering observed between replicates are typically similar or even larger than between biological conditions. For instance, in Figure 1B, I do not see any clustering when considering DBD1, DBD2, DBD+1, DBD+2.

Lanes 80-83: "KD replicates clustered together with DBD replicate 1 on both axes and with DBD replicate 2 on the y-axis. DBD+ replicates, on the other hand, clustered away from both KD and DBD replicates. These observations suggest that the global chromatin structure of DBD replicates is more similar to KD than DBD+ replicates."

When replacing DBD replicate 1 with DBD replicate 2, their statement would not be true anymore.

Additional replicates to clarify this aspect seem absolutely necessary since those data are paving the way for the entire manuscript.

Similarly:<br /> - In Figure 1C, how would the result look when comparing DBD2/KD2/DBD+2? Same when comparing DBD 1 with KD1 and DBD+1. Would the difference go in the same direction?<br /> - Figure 1D-E. How would these plots look like when comparing each replicate to each other's? How much difference would be observed when comparing, for instance, DBD1/DBD2 ? or DBD1/DBD+1?<br /> - Figure 2: again, how would these analyses look like when performing the analysis with only DBD1/DBD+1/KD1 or DBD2/DBD+2/KD?

Another major question is the stability of EWS-FLI DBD vs EWS-FLI DBD+ proteins. Indeed, it seems that they have more FLAG (i.e., EWS-FLI) peaks in the DBD+ condition compared to the DBD condition (Figure 2B). In the WB, FLAG intensities seem also higher (2/3 replicates) in DBD+ condition compared to the DBD condition (Figure S1B).

Would it be possible that DBD+ is just more expressed or more stable than DBD? The higher stability of the re-expressed DBD+ could also partially explain their results independently of the 3D conformational change. In other words, can they exclude that DBD+ and DBD binding are not related to their respective protein stability or their global re-expression levels?

Surprisingly, WB FLI bands in DBD+ conditions are systematically (3/3 replicates) fainter than in DBD conditions (Figure S1B). How do the authors explain these opposite results between FLI and FALG in the WB?

Reviewer #2 (Public Review):

Summary:

The manuscript by Bayanjargal et al. entitled "The DBD-alpha4 helix of EWS::FLI is required for GGAA microsatellite binding that underlies genome regulation in Ewing sarcoma" reports on the critical role of a small alpha helix in the DNA binding domain (DBD) of the FLI1 portion of EWS::FLI1 that is critical for binding to repetitive stretches of GGAA-motifs, i.e. GGAA microsatellites, which serve as potent neoenhancers in Ewing sarcoma.

Strengths:

The paper is generally well-written, and easy to follow and the data presented are of high quality, well-described and underpin the conclusions of the authors. The report sheds new light on how EWS::FLI1 mechanistically binds to and activates GGAA microsatellite enhancers, which is of importance to the field.

Weaknesses:

While there are no major weaknesses in this paper, there are a few minor issues that the authors may wish to address:

(1) While the official protein symbol for the gene EWSR1 is indeed EWS, the protein symbol for the gene FLI1 is identical, i.e. FLI1. The authors nominate the fusion oncoprotein EWS::FLI1 (even in the title) but it appears more adequate to use EWS::FLI1.

(2) The used cell lines should be spelled according to their official nomenclature (e.g. A-673 instead of A673).

(3) It appears as if the vast majority of results were generated in a single Ewing sarcoma cell line (A-673) which is an atypical Ewing sarcoma cell line harboring an activating BRAF mutation and may be genomically quite unstable as compared to other Ewing sarcoma cell lines (Kasan et al. 2023 preprint at bioRxiv https://www.biorxiv.org/content/10.1101/2023.11.20.567802v1). Hence, it may be supportive for the paper to recapitulate/cross-validate a few key results in other Ewing sarcoma cell lines, e.g. by using EWS::ERG-positive cell lines. Perhaps the authors could make use of available published data.

(4) Figure 6 and Supplementary Figure 5 are very interesting but focus on two selected target genes of the fusion (FCGRT and CCND1). It would be interesting to see whether these findings also extend to common EWS::ETS transcriptional signatures that have been reported. The authors could explore their data and map established consensus EWS::ETS signatures to investigate which other hubs might be affected at relevant target genes.

(5) Table 1 is a bit hard to read. In my opinion, it is not necessary to display P-values with up to 8 decimal positions. The gene symbols should be displayed in italic font.

eLife assessment

This important manuscript details the characterization of ClpL from L. monocytogenes as an effective and autonomous AAA+ disaggregase that provides enhanced heat resistance to this food-borne pathogen. Supported by compelling evidence, the authors demonstrate that ClpL has DnaK-independent disaggregase activity towards a variety of aggregated model substrates, which is more potent than that observed with the endogenous canonical DnaK/ClpB bi-chaperone system. The work will be of broad interest to microbiologists and biochemists.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This work describes the mechanism of protein disaggregation by the ClpL AAA+ protein of Listeria monocytogenes. Using several model subtrate proteins the authors first show that ClpL possesses a robust disaggregase activity that does not further require the endogenous DnaK chaperone in vitro. In addition, they found that ClpL is more thermostable than the endogenous L. monocytogenes DnaK and has the capacity to unfold tightly folded protein domains. The mechanistic basis for the robust disaggregase activity of ClpL was also dissected in vitro and in some cases, supported by in vivo data performed in chaperonedeficient E. coli strains. The data presented show that the two AAA domains, the pore-2 site and the N-terminal domain (NTD) of ClpL are critical for its disaggregase activity. Remarkably, grafting the NTD of ClpL to ClpB converted ClpB into an autonomous disaggregase, highlighting the importance of such a domain in the DnaK-independent disaggregation of proteins. The role of the ClpL NTD domain was further dissected, identifying key residues and positions necessary for aggregate recognition and disaggregation. Finally, using sets of SEC and negative staining EM experiments combined with conditional covalent linkages and disaggregation assays the authors found that ClpL shows significant structural plasticity, forming dynamic hexameric and heptameric active single rings that can further form higher assembly states via their middle domains.

Strengths:

The manuscript is well-written and the experimental work is well executed. It contains a robust and complete set of in vitro data that push further our knowledge of such important disaggregases. It shows the importance of the atypical ClpL N-terminal domain in the disaggregation process as well as the structural malleability of such AAA+ proteins. More generally, this work expands our knowledge of heat resistance in bacterial pathogens.

Weaknesses:

There is no specific weakness in this work, although it would have helped to have a drawing model showing how ClpL performs protein disaggregation based on their new findings. The function of the higher assembly states of ClpL remains unresolved and will need further extensive research. Similarly, it will be interesting in the future to see whether the sole function of the plasmid-encoded ClpL is to cope with general protein aggregates under heat stress.

We thank the reviewer for the positive evaluation. We agree with the reviewer that it will be important to test whether ClpL can bind to and process non-aggregated protein substrates. Our preliminary analysis suggests that the disaggregation activity of ClpL is most relevant in vivo, pointing to protein aggregates as main target.

We also agree that the role of dimers or tetramers of ClpL rings needs to be further explored. Our initial analysis suggests a function of ring dimers as a resting state. It will now be important to study the dynamics of ClpL assembly formation and test whether substrate presence shifts ClpL assemblies towards an active, single ring state.

Reviewer #2 (Public Review):

The manuscript by Bohl et al. is an interesting and carefully done study on the biochemical properties and mode of action of potent autonomous AAA+ disaggregase ClpL from Listeria monocytogenes. ClpL is encoded on plasmids. It shows high thermal stability and provides Listeria monocytogenes food-pathogen substantial increase in resistance to heat. The authors show that ClpL interacts with aggregated proteins through the aromatic residues present in its N-terminal domain and subsequently unfolds proteins from aggregates translocating polypeptide chains through the central pore in its oligomeric ring structure. The structure of ClpL oligomers was also investigated in the manuscript. The results suggest that mono-ring structure and not dimer or trimer of rings, observed in addition to mono-ring structures under EM, is an active species of disaggregase.

Presented experiments are conclusive and well-controlled. Several mutants were created to analyze the importance of a particular ClpL domain.

The study's strength lies in the direct comparison of ClpL biochemical properties with autonomous ClpG disaggregase present in selected Gram-negative bacteria and well-studied E. coli system consisting of ClpB disaggregase and DnaK and its cochaperones. This puts the obtained results in a broader context.

We thank the reviewer for the detailed comments. There are no specific weaknesses indicated in the public review.

Reviewer #3 (Public Review):

Summary:

This manuscript details the characterization of ClpL from L. monocytogenes as a potent and autonomous AAA+ disaggregase. The authors demonstrate that ClpL has potent and DnaKindependent disaggregase activity towards a variety of aggregated model substrates and that this disaggregase activity appears to be greater than that observed with the canonical DnaK/ClpB co-chaperone. Furthermore, Lm ClpL appears to have greater thermostability as compared to Lm DnaK, suggesting that ClpL-expressing cells may be able to withstand more severe heat stress conditions. Interestingly, Lm ClpP can provide thermotolerance to E. coli that have been genetically depleted of either ClpB or in cells expressing a mutant DnaK103. The authors further characterized the mechanisms by which ClpL interacts with protein aggregates, identifying that the N-terminal domain of ClpL is essential for disaggregase function. Lastly, by EM and mutagenesis analysis, the authors report that ClpL can exist in a variety of larger macromolecular complexes, including dimer or trimers of hexamers/heptamers, and they provide evidence that the N-terminal domains of ClpL prevent dimer ring formation, thus promoting an active and substrate-binding ClpL complex. Throughout this manuscript the authors compare Lm ClpL to ClpG, another potent and autonomous disaggregase found in gram-negative bacteria that have been reported on previously, demonstrating that these two enzymes share homologous activity and qualities. Taken together this report clearly establishes ClpL as a novel and autonomous disaggregase.

Strengths:

The work presented in this report amounts to a significant body of novel and significant work that will be of interest to the protein chaperone community. Furthermore, by providing examples of how ClpL can provide in vivo thermotolerance to both E. coli and L. gasseri the authors have expanded the significance of this work and provided novel insight into potential mechanisms responsible for thermotolerance in food-borne pathogens.

Weaknesses:

The figures are clearly depicted and easy to understand, though some of the axis labeling is a bit misleading or confusing and may warrant revision. While I do feel that the results and discussion as presented support the authors' hypothesis and overall goal of demonstrating ClpL as a novel disaggregase, interpretation of the data is hindered as no statistical tests are provided throughout the manuscript. Because of this only qualitative analysis can be made, and as such many of the concluding statements involving pairwise comparisons need to be revisited or quantitative data with stats needs to be provided. The addition of statistical analysis is critical and should not be difficult, nor do I anticipate that it will change the conclusions of this report.

We thank the reviewer for the valid criticism. We addressed the major concern of the reviewer and added the requested statistical analysis to all relevant figures. The analysis confirms our conclusions. We also followed the advice of the reviewer and revised axis labeling to increase clarity.

Reviewer #1 (Recommendations For The Authors):

• It would really help to have a model showing how ClpL performs protein disaggregation based on their findings.

We show that ClpL exerts a threading activity that is fueled by ATP hydrolysis in both AAA domains and executed by pore-located aromatic residues. The basic disaggregation mechanism of ClpL therefore does not differ from ClpB and ClpG disaggregases. Similarly, the specificity of ClpL towards protein aggregates is based on simultaneous interactions of multiple N-terminal domains with the aggregate surface. We could recently describe a similar mode of aggregate recognition for ClpG [1]. We therefore prefer not to add a model to the manuscript. We are currently in preparation of a review that includes the characterization of the novel bacterial disaggregases and will present models there as we consider a review article as more appropriate for such illustrations.

• AAA2 domain of ClpL in Fig 3E should be the same color as in Fig 1A.

We used light grey instead of dark grey for the ClpL AAA2 domain in Fig 3E, to distinguish between ClpL and ClpB AAA domains. This kind of illustration allows for clearer separation of both AAA+ proteins and the fusion construct LN-ClpB*. We therefore prefer keeping the color code.

• Partial suppression of the dnaK mutant could be added in the main manuscript Figure.

The main figure 3 is already very dense and we therefore prefer showing respective data as part of a supplementary figure.

• It would have been interesting to know if the robust autonomous disaggregation activity of ClpL would be sufficient to rescue the growth of more severe E. coli chaperone mutants, like dnaK tig for example. Did the authors test this?

We tested whether expression of clpL can rescue growth of E. coli dnaK103 mutant cells at 40°C on LB plates. This experiment is different from the restoration of heat resistance in dnaK103 cells (Figure 3, figure supplement 2A), as continuous growth at elevated temperatures (40°C) is monitored instead of cell survival upon abrupt severe heat shock (49°C). We did not observe rescue of the temperature-sensitive growth phenotype (40°C) of dnaK103 cells upon clpL expression, though expression of clpG complemented the temperature-sensitive growth phenotype (see Author response image 1 below). This finding points to differences in chaperone activities of ClpL and ClpG. It also suggests that ClpL activity is largely restricted to heat-shock generated protein aggregates, enabling ClpL to complement the missing disaggregation function of DnaK but not other Hsp70 activities including folding and targeting of newly synthesized proteins. We believe that dissecting the molecular reasons for differences in ClpG and ClpL complementation activities should be part of an independent study and prefer showing the growth-complementation data only in the response letter.

Author response image 1.

Serial dilutions (10-1 – 10-6) of E. coli dnaK103 mutant cells expressing E. coli dnaK, L. monocytogenes clpL or P. aeruginosa clpG were spotted on LB plates including the indicated IPTG concentrations. Plates were incubated at 30°C or 40°C for 24 h. p: empty vector control.

Reviewer #2 (Recommendations For The Authors):

Based on results presented in Fig. 2B the authors conclude "that stand-alone disaggregases ClpL and ClpG but not the canonical KJE/ClpB disaggregase exhibit robust threading activities that allow for unfolding of tightly folded domains" (page 5 line 209). In this experiment, the threading power of disaggregases was assessed by monitoring YFP fluorescence during the disaggregation of aggregates formed by fusion luciferase-YFP protein. In my opinion, the results of the experiment depend not only on the threading power of disaggregases but also on the substrate recognition by analyzed disaggregating systems and/or processivity of disaggregases. N-terminal domain in the case of ClpL and KJE chaperones in the case of the KJE/ClpB system are involved in recognition. This is not discussed in the manuscript and the obtained result might be misinterpreted. The authors have created the LN-ClpB* construct (N-terminal domain of ClpL fused to derepressed ClpB) (Fig. 3 E and F). In my opinion, this construct should be used as an additional control in the experiment in Fig. 2 B. It possesses the same substrate recognition domain and therefore the direct comparison of disaggregases threading power might be possible.

We performed the requested experiment (new Figure 3 - figure supplement 2D). We did not observe unfolding of YFP by LN-ClpB. Sínce ClpL and LN-ClpB do not differ in their aggregate targeting mechanisms, this finding underlines the differences in threading power between ClpL and activated (derepressed) ClpB. It also suggests that the AAA threading motors and the aggregate-targeting NTD largely function independently.

Presented results suggest that tetramer and dimer of rings might be a "storage form" of disaggregase. It would be interesting to analyze the thermotolerance and/or phenotype of ClpL mutants that do not form tetramer and dimer (E352A). This variant possesses similar to WT disaggregation activity but does not form dimers and tetramers. If in vivo the differences are observed (for example toxicity of the mutant), the "storage form" hypothesis will be probable.

When testing expression of clpL-MD mutants (E352A, F354A), which cannot form dimers and tetramers of ClpL rings, in E. coli ∆clpB cells, we observed reduced production levels as compared to ClpL wildtype and speculated that reduced expression might be linked to cellular toxicity. We therefore compared spotting efficiencies of E. coli ∆clpB cells expression clpL, ∆NclpL or the clpL-MD mutants at different temperatures. Expression of clpL at high levels abrogated colony formation at 42°C (new Figure 6 - figure supplement 3). ClpL toxicity was dependent on its NTD as no effect was observed upon expression of ∆N-clpL. ClpL-MD mutants (E352A, F354A) were expressed at much lower levels and exhibited strongly increased toxicity as compared to ClpL-WT when produced at comparable levels (new Figure 6 – figure supplement 3). This implies a protective role of ClpL ring dimers and tetramers in the cellular environment by downregulating ClpL activity. We envision that the formation of ClpL assemblies restricts accessibility of the ClpL NTDs and reduces substrate interaction. Increased toxicity of ClpL-E352A and ClpL-F354A points to a physiological relevance of the dimers and tetramers of ClpL rings and is in agreement with the proposed function as storage forms. We added this potential role of ClpL ring assemblies to the discussion section. Due to the strongly reduced production levels of ClpL MD mutants and their enhanced toxicity at elevated temperatures we did not test for their ability to restore thermotolerance in E. coli ∆clpB cells.

Figure 6G and Figure 6 -figure supplement 2 - it is not clear what is the difference in the preparation of WT and WTox forms of ClpL.

ClpL WT was purified under reduced conditions (+ 2 mM DTT), whereas WTox was purified in absence of DTT, thus serving as control for ClpL-T355C, which forms disulfide bonds upon purification without DTT. We have added respective information to the figure legend and the materials and methods section.

Page 5 line 250 - wrong figure citation. Instead of Figure 1 - Figure Supplement 2A should be Figure 3 - Figure Supplement 2A.

Page 5 line 251 - wrong figure citation. Instead of Figure 1 - Figure Supplement 2B/C should be Figure 3 - Figure Supplement 2B/C.

Page 7 line 315 - wrong figure citation. Instead of Figure 4F, it should be Figure 4G Figure 1 - Figure Supplement 2E - At first glance, this Figure does not correspond to the text and is confusing. It would be nice to have bars for Lm ClpL activity in the figure. Alternatively, the description of the y-axis might be changed to "relative to Lm ClpL disaggregation activity" instead of "relative disaggregation activity". One has to carefully read the figure legend to find out that 1 corresponds to Lm ClpL activity.

We have corrected all mistakes and changed the description of y-axis (Figure 1 - figure Supplement 2E) as suggested.

Reviewer #3 (Recommendations For The Authors):

(1) While the authors make many experimental comparisons throughout their study, no statistical tests are described or presented with their results or figures, nor are these statistical tests described in the methods. While the data as presented does appear to support the author's conclusions, without these statistical tests no meaningful conclusions from paired analysis can be drawn. Critically, please report these statistical tests. As a general suggestion please include the statistics (p-values) in the results section when presenting this data, as well as in the figure legends, as this will allow the reader to better understand the authors' presentation and interpretation of the data.

We have added statistical tests to all relevant figures. The analysis is confirming our former statements. We have further clarified our approach for the statistical analysis in the methods section. We report p-values in the results section, however, due to the volume of comparisons we did not add individual p-values to the figure legends but used standard labeling with stars.

(2) Some of the axis labels for the presented graphs are a bit misleading or confusing. Many describe a relative (%) disaggregation rate, but it is not clear from the methods or figure legends what this rate is relative to. Is it relative to non-denatured substrates, to no chaperone conditions, etc.? Is it possible to present the figures with the raw data rates/activity (ex. luciferase activity / time) vs. relative rates? I think that labeling these figure axes with "disaggregation rate" is a bit misleading as none of these experiments measure the actual rate of disaggregation of these model substrates per se (say by SEC-MALS or other biophysical measurements), but instead infer the extent of disaggregation by measuring a property of these substrates, i.e. luciferase activity or fluorescence intensity over time. Thus, labeling these figures with the appropriate axis for what is being measured, and then clarifying in the methods and results what is being inferred by these measurements, will help solidify the author's conclusions.

Relative (%) disaggregation rate usually refers to the disaggregation activity of ClpL wildtype serving as reference. We clarified this point in the revised text and respective figure legends. We now also refer to the process measured (e.g. relative refolding activity of aggregated Luciferase instead of relative disaggregation activity) as suggested by the reviewer and added clarifications to text and materials and methods.

Since we have many measurements for our most frequently used assays and have a reasonable estimate for the general variance within these assays, we found it reasonable to show activity data in relation to fixed controls. This reduces the impact of unspecific variance and thereby makes more accurate comparisons between different repetitions. The reference is now indicated in the axis title.

(3) The figures are well presented, clutter-free, and graphically easy to understand. Figure legends have sufficient information aside from the aforementioned statistical information and should include the exact number of independent replicates for each panel/experiment (ex. n=4), not just a greater than 3. While the figures do show each data point along with the mean and error, in some figures it is difficult to determine the number of replicate data points. Example figures 2c, 2d, and 3a. Also, please state whether the error is std. error or SEM.

While we agree, that this is valuable information, we fear that overloading the figure legends with information may take a toll on the readability. We therefore decided to append the number of replicates for each experiment in a separate supplementary table (Table S2). The depicted error is showing the SD and not the SEM, which we also specified in the figure legends.

(4) There are various examples throughout the results where qualitative descriptors are used to describe comparisons. Examples of this are "hardly enhanced" (Figure 1) and "partially reduced" (Figure 6). While this is not necessarily wrong, qualitative descriptions of comparisons in this manner would require further explanation. What is the definition of "hardly" or "partially"? My recommendation is to just state the data quantitatively, such as "% enhanced" or "reduced by x", this way there is no misinterpretation. Examples of this can be found in Figures 6C-G. This would require a full statistical overview and presentation of these stats in the results.

We followed the reviewer`s advice and no longer use the terms criticized (e.g. “hardly enhanced”). We instead provide the requested quantifications in the text.

Questions for Figures:

Figures 1B and 1C:

(1) Is the disaggregase activity of ClpL towards heat-denatured luciferase and GFP ATPdependent? While the authors later in the manuscript show that mutations within the Walker B domains dramatically impair reactivation (disaggregation) of denatured luciferase, this does not rule out an ATP-independent effect of these mutations. Thus, the authors should test whether disaggregase activity is observed when wild-type ClpL is incubated with denatured substrates without ATP present or in the presence of ADP only.

We tested for ClpL disaggregation activity in absence of nucleotide and presence of ADP only (new Figure 1 – figure supplement 2A). We did not observe any activity, demonstrating that ClpL activity depends on ATP binding and hydrolysis (see also Figure 3 – figure supplement 1D: ATPase-deficient ClpL-E197A/E530A is lacking disaggregation activity).

(2) The authors suggest that a reduction in disaggregase activity observed in samples combining Lm ClpL and KJE (Figure 1C, supp. 1C-E) could be due to competition for protein aggregate binding as observed previously with ClpG. Did the authors test this directly by pulldown assay or another interaction-based assay? While ClpL and ClpG appear to work in a similar manner, it would be good to confirm this. Also, clarification on how this competition operates would be useful. Is it that ClpL prevents aggregates from interacting with KJE, or vice versa?

We probed for binding of ClpL to aggregated Malate Dehydrogenase in the presence of L. monocytogenes or E. coli Hsp70 (DnaK + respective J-domain protein DnaJ) by a centrifugation-based assay. Here, we used the ATPase-deficient ClpL-E197A/E530A (ClpLDWB) mutant, ensuring stable substrate interaction in presence of ATP. We observe reduced binding of ClpL-DWB to protein aggregates in presence of DnaK/DnaJ (new Figure 1 – figure supplement 2G). This finding indicates that both chaperones compete for binding to aggregated proteins and explains inhibition of ClpL disaggregation activity in presence of Hsp70.

(3) Related to the above, while incubation of aggregated substrates with ClpL and KJE does appear to reduce aggregase activity towards GFP (Figure 1c), α-glucosidase (Supp. 1C), and MDH (Supp. 1D), this doesn't appear to be the case towards luciferase (Figure 1b, Supp. 1b). Furthermore, ClpL aggregase activity is reduced towards luciferase when combined with E. coli KJE (Supp. 1e) but not with Lm KJE (Figure 1b). The authors provide no commentary or explanation for these observations. Furthermore, these results complicate the concluding statement that "combining ClpL with Lm KJE always led to a strong reduction in disaggregation activity ... ".

We suggest that the differing inhibitory degrees of the KJE system on ClpL disaggregation activities reflect diverse binding affinities of KJE and ClpL to the respective aggregates. While we usually observe strong inhibition of ClpL activity in presence of KJE, this is different for aggregated Luciferase. This points to specific structural features of Luciferase aggregates or the presence of distinct binding sites on the aggregate surface that favour ClpL binding. We have added a respective comment to the revised manuscript.

The former statement that “combining ClpL with Lm KJE always led to a strong reduction in disaggregation activity” referred to aggregated GFP, MDH and α-Glucosidase for which a strong inhibition of ClpL activity was observed. We have specified this point.

Figures 1D and 1E:

(1) The authors conclude that the heat sensitivity of ΔClpL L. gasseri cells is because they do not express the canonical ClpB disaggregase. A good test to validate this would be to express KJE/ClpB in these Lg ΔClpL cells to see if heat-sensitivity could be fully or partially rescued.

We agree that such experiment would further strengthen the in vivo function of ClpL as alternative disaggregase. However, such approach would demand for co-expression of E. coli ClpB with the authentic E. coli DnaK chaperone system (KJE), as ClpB and DnaK cooperate in a species-specific manner [2-4]. This makes the experiment challenging, also because the individual components need to be expressed at a correct stochiometry. Furthermore, the presence of the authentic L. gasseri KJE system, which is likely competing with the E. coli KJE system for aggregate binding, will hamper E. coli KJE/ClpB disaggregation activity in L. gasseri. In view of these limitations, we would like to refrain from conducting such an experiment.

(2) The rationale for investigating Lg ClpL, and the aggregase activity assays are compelling and support the hypothesis that ClpL contributes to thermotolerance in multiple grampositive species. Though, from Figure 1d, why was only Lg ClpL investigated? It appears that S. thermophilus also lacks the canonical ClpB disaggregase and demonstrates ΔClpL heat sensitivity. There is also other Lactobacillus sp. presented that lack ClpB but were not tested for heat sensitivity. Why only test and move forward with L. gasseri? Lastly, L. mesenteroides is ClpB-negative but doesn't demonstrate ΔClpL heat sensitivity. Why?

We wanted to document high, partner-independent disaggregation activity for another ClpL homolog. We chose L. gasseri, as (i) this bacterial species lacks a ClpB homolog and (ii) a ∆clpL mutant exhibit reduced survival upon severe heat shock (thermotolerance phenotype), which is associated with defects in cellular protein disaggregation. The characterization of L. gasseri ClpL as potent disaggregase in vitro represents a proof-of-concept and allows to generalize our conclusion. We therefore did not further test S. thermophilus ClpL. L. mesenteroides encodes for ClpL but not ClpB, yet, a ∆clpL mutant has not yet been characterized in this species to the best of our knowledge. As we wanted to link ClpL in vitro activity with an in vivo phenotype, we did not characterize L. mesenteroides ClpL.

We agree with the reviewer that the characterization of additional ClpL homologs is meaningful and interesting, however, we strongly believe that such analysis should be part of an exhaustive and independent study.

Figures 2A and 2B:

(1) Figure 2B demonstrates that both ClpL and ClpG, but not the canonical KJE/ClpB, are able to unfold YFP during the luciferase disaggregation process, suggesting that ClpL and ClpG exhibit stronger threading activity. A technical question, can luciferase activity be measured alongside in the same assay sample? If so, would you expect to observe a concomitant increase in luciferase activity as YFP fluorescence decreases?

KJE/ClpB can partially disaggregate and refold aggregated Luciferase-YFP without unfolding YFP during the disaggregation reaction [5]. YFP unfolding is therefore not linked to refolding of aggregated Luciferase-YFP. On the other hand, unfolding of YFP during disaggregation can hamper the refolding of the fused Luciferase moiety as observed for the AAA+ protein ClpC in presence of its partner MecA [5]. These diverse effects make the interpretation of LuciferaseYFP refolding experiments difficult as the degree of YFP unfolding activity does not necessarily correlate with the extend of Luciferase refolding. We therefore avoided to perform the suggested experiment.

Figure 2C and 2D:

(1) Thermal shift assays for ClpL, ClpG, and DnaK were completed with various nucleotides. Were these experiments also completed with samples in their nucleotide-free apo state? Also, while all these chaperones are ATPases, the nucleotides used differ, but no explanation is provided. Comparison should be made of these ATPases bound to the same molecules.

We did not monitor thermal stabilities of chaperones without nucleotide as such state is likely not relevant in vivo. We used ATPγS in case of ClpL to keep the AAA+ protein in the ATPconformation. ATP would be rapidly converted to ADP due to the high intrinsic ATPase activity of ClpL. In case of DnaK ATPγS cannot be used as it does not induce the ATP conformation [6]. The low intrinsic ATPase activity of DnaK allows determining the thermal stability of its ATP conformation in presence of ATP. This is confirmed by calculating a reduced thermal stability of ADP-bound DnaK.

(2) The authors suggest that incubation at 55⁰C will cause unfolding of Lm DnaK, but not ClpL, providing ClpL-positive Lm cells disaggregase activity at 55⁰C. While the thermal shift assays in Figures 2C and 2D support this, an experiment to test this would be to heat-treat Lm DnaK and ClpL at 55⁰C then test for disaggregase activity using either aggregated luciferase or GFP as in Figure 1.

We followed the suggestion of the reviewer and incubated Lm ClpL and DnaK at 55-58°C in presence of ATP for 15 min prior to their use in disaggregation assays. We compared the activities of pre-heated chaperones with controls that were incubated at 30°C for 15 min. Notably, we did not observe a loss of DnaK disaggregation activity, suggesting that thermal unfolding of DnaK at this temperature is reversible. We provide these data as Figure 2 -figure supplement 1 and added a respective statement to the revised manuscript.

Figure 3B:

(1) The authors state that ATPase activity of ΔN-ClpL was "hardly affected", but from the data provided it appeared to result in an approximate 35% reduction. As discussed above, no stats are provided for this figure, but given the error bars, it is highly likely that this reduction is significant. Please perform this statistical test, and if significant, please reflect this in the written results as well as the figure. Lastly, if this reduction in ATPase activity is significant, why would this be so, and could this contribute to the reduction in aggregase activity towards luciferase and MDH observed in Figure 3A?

We applied statistical tests as suggested by the reviewer, showing that the reduction in ATPase activity of ∆N-ClpL is statistically significant. N-terminal domains of Hsp100 proteins can modulate ATPase activity as shown for the family member ClpB, functioning as auxiliary regulatory element for fine tuning of ClpB activity [7]. We speculate that the impact of the ClpL-NTD on the assembly state (stabilization of ClpL ring dimers) might affect ClpL ATPase activity. We would like to point out that other ClpL mutants (e.g. NTD mutant ClpL-Y51A; MDmutant ClpL-F354A) have a similarly reduced ATPase activity, yet exhibit substantial disaggregation activity (approx. 2-fold reduced compared to ClpL wildtype). In contrast ∆NClpL does not exhibit any disaggregation activity. This suggests that the loss of disaggregation activity is caused by a substrate binding defect but not by a partial reduction in ATPase activity. We added a comment on the reduced ATPase activity and also discuss its potential reasons in the discussion section.

(2) I think the authors' conclusion that deletion of the ClpL NTD does not contribute to structural defects of ClpL is premature given the apparent reduction in ATPase activity. Did the authors perform any biophysical analysis of ΔN-ClpL to confirm this conclusion? Thermal shift assays, Native-PAGE, or size-exclusion chromatography for aggregates would all be good assays to demonstrate that the wild-type and ΔN-ClpL have similar structural properties. Surprisingly, Figure 6 describes significant macromolecular changes associated with ΔN-ClpL such that it preferentially forms a dimer of rings. Furthermore, in Supp. Figure 6D the authors report that ΔN-ClpL appears to have an increased Tm as compared to WT- or ΔM-ClpL. The authors should reflect these observations as deletion of the ClpL NTD does appear to contribute to structural changes, though perhaps only at the macromolecular scale, i.e. dimerization of the rings.

We have characterized the oligomeric state of ∆N-ClpL by size exclusion chromatography (Figure 6 – figure supplement 1A) and negative staining electron microscopy (Figure 6C), both showing that it forms assemblies similar to ClpL wildtype. We did not observe an increased tendency of ∆N-ClpL to form aggregates and the protein remained fully soluble after several cycles of thawing and freezing. EM data reveal that ∆N-ClpL exclusively form ring dimers, suggesting that the NTDs destabilize MD-MD interactions. The stabilized interaction between two ∆N-ClpL rings can explain the increased thermal stability (Figure 6 – figure supplement 1D). We speculate that the ClpL NTDs either affect MD-MD interactions through steric hindrance or by directly contacting MDs. We have added a respective statement to the discussion section.

Figure 3C and 3D:

(1) Given the larger error in samples expressing ClpG (100) or ClpL (100) statistical analysis with p-values is required to make conclusions regarding the comparison of these samples vs. plasmid-only control. The effect of ΔN-ClpL vs. wild-type ClpL looks compelling and does appear to attenuate the ClpL-induced thermotolerance. This is nicely demonstrated in Figure 3D.

We quantified respective spot tests (new Figure 3E) and tested for statistical significance as suggested by the reviewer. We show that restoration of heat resistance is significant for the first 30 min. While we always observe rescue at later timepoints significance is lost here due to larger deviations in the number of viable cells and thus the degree of complementation.

Figure 3F:

(1) What is the role of the ClpB NTD? It appears to be dispensable for disaggregase activity, assuming that ClpB is co-incubated with KJE. A quick explanation of this domain in ClpB could be useful.

The ClpB NTD is not required for disaggregation activity, as ClpB is recruited to protein aggregates by DnaK, which interacts with the ClpB MDs. Still, two functions have been described for the ClpB NTD. First, it can bind soluble unfolded substrates such as casein [8]. This substrate binding function can increase ClpB disaggregation activity towards some aggregated model substrates (e.g. Glucose-6-phosphate dehydrogenase) [9]. However, NTD deletion usually does not decrease ClpB disaggregation activity and can even lead to an increase [7, 10, 11]. An increased disaggregation activity of ∆N-ClpB correlates with an enhanced ATPase activity, which is explained by NTDs stabilizing a repressing conformation of the ClpB MDs, which function as main regulators of ClpB ATPase activity [7]. We added a short description on the role of the ClpB NTD to the respective results section.

(2) The result of fusing the ClpL NTD to ClpB supports a role for this NTD in promoting autonomous disaggregase activity. What would you expect to observe if the fused Ln-ClpB protein was co-incubated with KJE? Would this further promote disaggregase activity, or potentially impair through competition? This experiment could potentially support the authors' hypothesis that ClpL and ClpB/KJE can compete with each other for aggregated substrates as suggested in Figure 1.

We have performed the suggested experiment using aggregated MDH as model substrate. We did not observe an inhibition of LN-ClpB disaggregation activity in presence of KJE. In contrast ClpL disaggregation activity towards aggregated MDH is inhibited upon addition of KJE due to competition for aggregate binding (Figure 1 – figure supplement 2D/F). Disaggregation activity of LN-ClpB in presence of KJE can be explained by functional cooperation between both chaperone systems, which involves interactions between aggregate-bound DnaK and the ClpB MDs of the LN-ClpB fusion construct. We prefer showing these data only in the response letter but not including them in the manuscript, as respective results distract from the main message of the LN-ClpB fusion construct: the ClpL NTD functions as autonomous aggregatetargeting unit that can be transferred to other Hsp100 family members.

Author response image 2.

LN-ClpB cooperates with DnaK in protein disaggregation. Relative MDH disaggregation activities of indicated disaggregation systems were determined. KJE: DnaK/DnaJ/GrpE. The disaggregation activity of Lm ClpL was set to 1. Statistical Analysis: Oneway ANOVA, Welch’s Test for post-hoc multiple comparisons. Significance levels: **p < 0.001. n.s.: not significant.

Figures 4E and 4F:

(1) While the effect of various NTD mutations follows a similar trend in regard to the impairment of ClpL-mediated disaggregation of luciferase and MDH, the degree of these effects does appear different. For example, patch A and C mutations reduce ClpL disaggregase activity towards luciferase (~60% / 50% reduction) vs. MDH (>90%) respectively. While these results do suggest a critical role for residues in patches A and C of ClpL, these substrate-specific differences are not discussed. Why would we expect a difference in the effect of these patch A/C ClpL mutations on different substrates?

We speculate that the aggregate structure and the presence or distributions of ClpL NTD binding sites differ between aggregated Luciferase and MDH. A difference between both aggregated model substrates was also observed when testing for an inhibitory effect of Lm KJE (and Ec KJE) on ClpL disaggregation activity (see comment above). We speculate that the mutated NTD residues make specific contributions to aggregate recognition. The severity of binding defects (and reduction of disaggregation activities) of these mutants will depend on specific features of the aggregated model substrates. We now point out that ClpL NTD patch mutants can differ in disaggregation activities depending on the aggregated model substrate used and refer to potential differences in aggregate structures.

(2) The authors suggest that the loss of disaggregation activity of selected NTD mutants could be linked to reduced binding to aggregated luciferase. While this is likely given that these mutations do not appear to affect ATPase activity (Supp. 4), it could be possible that these mutants can still bind to aggregated luciferase and some other mechanism may impair disaggregation. A pull-down assay would help to prove whether reduced binding is observed in these NTD ClpL mutants. This also needs to be confirmed for Supp. Figure 4.2H.

We have shown a strong correlation between loss of aggregate binding and disaggregation activity for several NTD mutants (Fig. 4G, Figure 4 – figure supplement 2H). We decided to perform the aggregate binding assay only with mutants that show a full but not a partial disaggregation defect as we made the experience that the centrifugation-based assay provides clear and reproducible results for loss-of-activity mutants but has limitations in revealing differences for partially affected mutants. This might be explained by the use of nonhydrolyzable ATPγS in these experiments, which strongly stabilizes substrate interactions, potentially covering partial binding defects. We agree with the reviewer that some ClpL NTD mutants might have additional effects on disaggregation activity by e.g. controlling substrate transfer to the processing pore site. We have added a respective comment to the revised manuscript.

(3) Supp. Figure 4.2H has no description in the figure legend. The Y-axes states % aggregate bound to chaperone. How was this measured? See the above comments for Figures 4E and 4F.

We apologize and added the description to the figure legend. The determination of % aggregate bound chaperone is based on the quantifications of chaperones present in the supernatant and pellet fractions after sample centrifugation. Background levels of chaperones in the pellet fractions in absence of protein aggregates were subtracted. We added this information to the materials and methods section.

Figure 6G:

The authors observed reduced disaggregase activity and ATPase activity of mutant T355C under both oxidative and reducing conditions. While this observation under oxidative conditions supports the authors' hypothesis, under reducing conditions (+DTT) we would expect the enzyme to behave similarly to wild-type ClpL unless this mutation has other effects. Can the authors please comment on this and provide an explanation or hypothesis?

The reviewer is correct, ClpL-T355C exhibit a reduced disaggregation activity (Figure 6 – figure supplement 2B). We observe a similar reduction in disaggregation activity for the ClpL MD mutant F354A, pointing to an auxiliary function of the MD in protein disaggregation. We have made a respective comment in the discussion section of the revised manuscript. How exactly ClpL MDs support protein disaggregation is currently unclear and will be subject of future analysis in the lab. We strongly believe that such analysis should be part of an independent study.

Discussion:

In the fourth feature, it is discussed that one disaggregase feature of ClpL is that it does not cooperate with the ClpP protease. While a reference is provided for the canonical ClpB, no data in this paper, nor a reference, is provided demonstrating that ClpL does not interact with ClpP. As discussed, it is highly unlikely that ClpL interacts with ClpP given that ClpL does not contain the IGL/F loops that mediate the interaction of ClpP with cochaperones, such as ClpX, but data or a reference is needed to make such a factual statement.

The absence of the IGL/F loop makes an interaction between ClpL and ClpP highly unlikely. However, the reviewer is correct, direct evidence for a ClpP-independent function of ClpL, though very likely, is not provided. We have therefore rephrased the respective statement: “Forth, novel disaggregases lack the specific IGL/F signature motif, which is essential for cooperation of other Hsp100 proteins with the peptidase ClpP. This feature is shared with the canonical ClpB disaggregase [12] suggesting that protein disaggregation is primarily linked to protein refolding.”.

References

(1) Katikaridis P, Simon B, Jenne T, Moon S, Lee C, Hennig J, et al. Structural basis of aggregate binding by the AAA+ disaggregase ClpG. J Biol Chem. 2023:105336.

(2) Glover JR, Lindquist S. Hsp104, Hsp70, and Hsp40: A novel chaperone system that rescues previously aggregated proteins. Cell. 1998;94:73-82.

(3) Krzewska J, Langer T, Liberek K. Mitochondrial Hsp78, a member of the Clp/Hsp100 family in Saccharomyces cerevisiae, cooperates with Hsp70 in protein refolding. FEBS Lett. 2001;489:92-6.

(4) Seyffer F, Kummer E, Oguchi Y, Winkler J, Kumar M, Zahn R, et al. Hsp70 proteins bind Hsp100 regulatory M domains to activate AAA+ disaggregase at aggregate surfaces. Nat Struct Mol Biol. 2012;19:1347-55.

(5) Haslberger T, Zdanowicz A, Brand I, Kirstein J, Turgay K, Mogk A, et al. Protein disaggregation by the AAA+ chaperone ClpB involves partial threading of looped polypeptide segments. Nat Struct Mol Biol. 2008;15:641-50.

(6) Theyssen H, Schuster H-P, Bukau B, Reinstein J. The second step of ATP binding to DnaK induces peptide release. J Mol Biol. 1996;263:657-70.

(7) Iljina M, Mazal H, Goloubinoff P, Riven I, Haran G. Entropic Inhibition: How the Activity of a AAA+ Machine Is Modulated by Its Substrate-Binding Domain. ACS chemical biology. 2021;16:775-85.

(8) Rosenzweig R, Farber P, Velyvis A, Rennella E, Latham MP, Kay LE. ClpB N-terminal domain plays a regulatory role in protein disaggregation. Proc Natl Acad Sci U S A. 2015;112:E6872-81.

(9) Barnett ME, Nagy M, Kedzierska S, Zolkiewski M. The amino-terminal domain of ClpB supports binding to strongly aggregated proteins. J Biol Chem. 2005;280:34940-5.

(10) Beinker P, Schlee S, Groemping Y, Seidel R, Reinstein J. The N Terminus of ClpB from Thermus thermophilus Is Not Essential for the Chaperone Activity. J Biol Chem. 2002;277:47160-6.

(11) Mogk A, Schlieker C, Strub C, Rist W, Weibezahn J, Bukau B. Roles of individual domains and conserved motifs of the AAA+ chaperone ClpB in oligomerization, ATP-hydrolysis and chaperone activity. J Biol Chem. 2003;278:15-24.

(11) Weibezahn J, Tessarz P, Schlieker C, Zahn R, Maglica Z, Lee S, et al. Thermotolerance Requires Refolding of Aggregated Proteins by Substrate Translocation through the Central Pore of ClpB. Cell. 2004;119:653-65.

Reviewer #1 (Public Review):

Summary:

This work describes the mechanism of protein disaggregation by the ClpL AAA+ protein of Listeria monocytogenes. Using several model subtrate proteins the authors first show that ClpL possesses a robust disaggregase activity that does not further require the endogenous DnaK chaperone in vitro. In addition, they found that ClpL is more thermostable than the endogenous L. monocytogenes DnaK and has the capacity to unfold tightly folded protein domains. The mechanistic basis for the robust disaggregase activity of ClpL was also dissected in vitro and in some cases, supported by in vivo data performed in chaperone-deficient E. coli strains. The data presented show that the two AAA domains, the pore-2 site and the N-terminal domain (NTD) of ClpL are critical for its disaggregase activity. Remarkably, grafting the NTD of ClpL to ClpB converted ClpB into an autonomous disaggregase, highlighting the importance of such a domain in the DnaK-independent disaggregation of proteins. The role of the ClpL NTD domain was further dissected, identifying key residues and positions necessary for aggregates recognition and disaggregation. Finally, using sets of SEC and negative staining EM experiments combined with conditional covalent linkages and disaggregation assays the authors found that ClpL shows significant structural plasticity, forming dynamic hexameric and heptameric active single rings that can further form higher assembly states via their middle domains.

Strengths:

The manuscript is well written and the experimental work well executed. It contains a robust and complete set of in vitro data that push further our knowledge of such important disaggregases. It shows the importance of the atypical ClpL N-terminal domain in the disaggregation process as well as the structural malleability of such AAA+ proteins. More generally, this work expands our knowledge of heat resistance in bacterial pathogens.

Weaknesses:

There is no specific weakness in this work, although it would have helped to have a drawing model showing how ClpL performs protein disaggregation based on their new findings. The function of the higher assembly states of ClpL remains unresolved and will need further extensive research. Similarly, it will be interesting in the future to see whether the sole function of the plasmid encoded ClpL is to cope with general protein aggregates under heat stress.

Reviewer #2 (Public Review):

The manuscript by Bohl et al. is an interesting and carefully done study on the biochemical properties and mode of action of potent autonomous AAA+ disaggregase ClpL from Listeria monocytogenes. ClpL is encoded on plasmids. It shows high thermal stability and provides Listeria monocytogenes food-pathogen substantial increase in resistance to heat. The authors show that ClpL interacts with aggregated proteins through the aromatic residues present in its N-terminal domain and subsequently unfolds proteins from aggregates translocating polypeptide chains through the central pore in its oligomeric ring structure. The structure of ClpL oligomers was also investigated in the manuscript. The results suggest that mono-ring structure and not dimer or tetramer of rings, observed in addition to mono-ring structures under EM, is an active specie of disaggregase. In the revised version additional data is presented suggesting that dimer or tetramer of ClpL rings play a protective role in cell by restricting ClpL activity.

Presented experiments are conclusive and well controlled. I think the presentation and discussion of results are better in revised version.<br /> The study's strength lies in the direct comparison of ClpL biochemical properties with autonomous ClpG disaggregase present in selected Gram-negative bacteria and well-studied E. coli system consisting of ClpB disaggregase and DnaK and its cochaperones. This puts the results in a broader context.

Reviewer #3 (Public Review):

Summary:

This manuscript details the characterization of ClpL from L. monocytogenes as a potent and autonomous AAA+ disaggregase. The authors demonstrate that ClpL has potent and DnaK-independent disaggregase activity towards a variety of aggregated model substrates, and that this disaggregase activity appears to be greater than that observed with the canonical DnaK/ClpB co-chaperone. Furthermore, LmClpL appears to have greater thermostability as compared to LmDnaK, suggesting that ClpL-expressing cells may be able to withstand more severe heat stress conditions. Interestingly, LmClpL can provide thermotolerance to E. coli that have been genetically depleted of either ClpB or in cells expressing a mutant DnaK103. The authors further characterized the mechanisms by which ClpL interacts with protein aggregates, identifying that the N-terminal domain of ClpL is essential for disaggregase function. Lastly, by EM and mutagenesis analysis the authors report that ClpL can exist in a variety of larger macromolecular complexes, including dimer or trimers of hexamers/heptamers, and they provide evidence that the N-terminal domains of ClpL prevent dimer ring formation, thus promoting an active and substrate-binding ClpL complex. Throughout this manuscript the authors compare LmClpL to ClpG, another potent and autonomous disaggregase found in gram-negative bacteria that has been reported on previously, demonstrating that these two enzymes share homologous activity and qualities. Taken together this report clearly establishes ClpL as a novel and autonomous disaggregase.

Analysis:

The work presented in this report amounts to a significant body of novel and significant work that will be of interest to protein chaperone community. Furthermore, by providing examples of how ClpL can provide in vivo thermotolerance to both E. coli and L. gasseri the authors have expanded the significance of this work and provides novel insight into potential mechanisms responsible for thermotolerance in food-borne pathogens. The figures are clearly depicted, well-labeled, and easy to understand, and the manuscript is well-written. Experimentally the work was performed to a high standard with excellent controls, aiding in the ability for the audience to understand the major findings and conclusions. Additionally, the authors have effectively and efficiently expanded on their work through the peer review process, further increasing the understandability and significance of their work. Overall, the data presented, and analysis thereof, support the authors' conclusions, and thus this study represents an important addition to our understanding of molecular chaperone biochemistry. Lastly, this study establishes new avenues for research into autonomous disaggregates, their role in in vivo thermotolerance, and the mechanisms by which AAA+ chaperones recognize and interact with substrate proteins.

Author Response

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

eLife assessment

This fundamental study advances our understanding of the cell specific treatment of cone photoreceptor degeneration by Txnip. The evidence supporting the conclusions is convincing with rigorous genetic manipulation of Txnip mutations, however, there are a few areas in which the article may be improved through further analysis and application of the data. The work will be of broad interest to vision researchers, cell biologists and biochemists.

Reviewer #1 (Public Review):

Summary:

This is a follow-up study to the authors' previous eLife report about the roles of an alpha-arrestin called protein thioredoxin interacting protein (Txnip) in cone photoreceptors and in the retinal pigment epithelium. The findings are important because they provide new information about the mechanism of glucose and lactate transport to cone photoreceptors and because they may become the basis for therapies for retinal degenerative diseases.

Strengths:

Overall, the study is carefully done and, although the analysis is fairly comprehensive with many different versions of the protein analyzed, it is clearly enough described to follow. Figure 4 greatly facilitated my ability to follow, understand and interpret the study.

Weaknesses:

I have just one concern that I would like the authors to address. It is about the text that begins at line 133: "We assayed their ability to clear GLUT1 from the RPE surface (Figure 2A)". Please provide more details about this. From the figure it appears that n = 1 for this experiment, but given how careful the authors are with these types of studies that seems unlikely. How did the authors quantify the ability to clear GLUT1 from the surface? Was it cleared from both the apical and basal surface? (It is hard to resolve the apical and basal surfaces in the images provided). The experiments shown in Fig. 1H and Fig. 1I of PMID 31365873 shows how GLUT1 disappears only from the apical surface (under the conditions of that experiment and through the mechanism described in their text). It would be helpful for the authors to discuss their current results in the context of that experiment.

We repeated all eight AAV-Best1-Txnip alleles for RPE GLUT1 staining with more than three eyes of each condition. We also quantified the GLUT1 intensity on the RPE basal surface. A new Figure 2-figure supplement 1 with these data has been added to this submission. The results and conclusions are similar to those in our initial submission.

As mentioned in our provisional responses: GLUT1 on the basal surface of the RPE is more easily scored than that on the apical surface. The photoreceptor inner segments and Müller glia microvilli also have GLUT1, and their processes are juxtaposed and/or intertwined with the apical processes of the RPE, making the apical process GLUT1 staining of the RPE much more difficult to score. In some sections where the RPE and the retina separate, we can score the apical process GLUT1 staining of the RPE, but we do not always have this situation in our sections. The current quantification in the new Figure 2-figure supplement 1 thus concerns only the basal staining.

As a separate issue, Reviewer #1 mentioned the work of another group (Wang et al., 2019, PMID: 31365873), which claimed that, on the apical surface of the RPE, GLUT1 is down-regulated in a RP mouse strain, RhoP23H. We have not consistently observed such a down-regulation of GLUT1 in other RP mouse strains such as rd1, rd10 or Rho-/- (unpublished data; see review Xue and Cepko, 2023, PMID: 37460158). However, as we pointed out above, it is difficult to score GLUT1 staining on the RPE apical surface. It is even more difficult in the degenerating retina where RPE and photoreceptor processes degenerate. For reference, one can see images of degenerating RPE apical processes in Wu et al. 2021 (PMID: 33491671).

Reviewer #2 (Public Review):

The hard work of the authors is much appreciated. With overexpression of a-arrestin Txnip in RPE, cones and the combined respectively, the authors show a potential gene agnostic treatment that can be applied to retinitis pigmentosa. Furthermore, since Txnip is related to multiple intracellular signaling pathway, this study is of value for research in the mechanism of secondary cone dystrophy as well.

There are a few areas in which the article may be improved through further analysis and application of the data, as well as some adjustments that should be made in to clarify specific points in the article.

Reviewer #3 (Public Review):

Summary:

Xue et al. extended their groundbreaking discovery demonstrating the protective effect of Txnip on cone photoreceptor survival. This was achieved by investigating the protection of cone degeneration through the overexpression of five distinct mutated variants of Txnip within the retinal pigment epithelium (RPE). Moreover, the study explored the roles of two proteins, HSP90AB1 and Arrdc4, which share similarities or associations with Txnip. They found the protection of Txnip in RPE cells and its mechanism is different from its protection in cone cells. These discoveries have significant implications for advancing our understanding of the mechanisms underlying Txnip's protection on cone cells.

Strengths: (1) Identify the roles of different Txnip mutations in RPE and their effects on the expression of glucose transporter

(2) Dissect the mechanism of Txnip in RPE vs Cone photoreceptors in retinal degeneration models.

(3) Explore the functions of ARrdc4, a protein similar to Txnip and HSP90AB1 in cone degeneration.

Weaknesses:

(1) Arrdc4 has deleterious effect on cone survival but no discussion on its mechanism.

(2) Inhibition of HSP90 is known to cause retinal generation. It is unclear why inhibition enhances the protection of Txnip.

As mentioned in our provisional responses, little was known about the function of Arrdc4 or HSP90AB1 in cones. We summarize some of the recent discoveries regarding these two proteins in the new Discussion:

“Arrdc4, the most similar α-arrestin protein to Txnip that also has Arrestin N- and C- domains, accelerated RP cone death when transduced via AAV (Figure 1). This observation suggests that Txnip has unique functions that protect RP cones. Recently, Arrdc4 has been proposed to be critical for liver glucagon signaling, which could be negated by insulin (Dagdeviren et al. 2023). The implication of this potential role in RP cone survival is unclear, but interestingly, the activation of the insulin/mTORC1 pathway is beneficial to RP cone survival (Punzo et al. 2009; Venkatesh et al. 2015).”

“Little is known about the function of HSP90AB1. Knocking down Hsp90ab1 improved mitochondrial metabolism of skeletal muscle in a diabetic mouse model (Jing et al. 2018). Knocking out HSP90AA1, a paralog of HSP90AB1 which has 14% different amino acids, led to rod death and correlated with PDE6 dysregulation (Munezero et al. 2023). Inhibiting HSP90AA1 with small molecules transiently delayed cone death in human retinal organoids under low glucose conditions (Spirig et al. 2023). However, the exact role of HSP90AA1 in photoreceptors needs to be clarified, and the implications for HSP90AB1 in RP cones are still unclear. ”

In addition, we used AlphaFold Multimer, an AI algorithm based on AlphaFold-2, to explore the possible interaction between TXNIP, PARP1 and HSP90AB1 in the revision. One of the predicted models is shown as the new Figure 5-figure supplement 2. The C-terminus of Txnip is predicted to link HSP90AB1 and PARP1 together in this model.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I have just one concern that I would like the authors to address. It is about the text that begins at line 133: "We assayed their ability to clear GLUT1 from the RPE surface (Figure 2A)". Please provide more details about this. From the figure it appears that n = 1 for this experiment, but given how careful the authors are with these types of studies that seems unlikely. How did the authors quantify the ability to clear GLUT1 from the surface? Was it cleared from both the apical and basal surface? (It is hard to resolve the apical and basal surfaces in the images provided). The experiments shown in Fig. 1H and Fig. 1I of PMID 31365873 shows how GLUT1 disappears only from the apical surface (under the conditions of that experiment and through the mechanism described in their text). It would be helpful for the authors to discuss their current results in the context of that experiment.

See our responses to Review #1’s public review section above.

Also, is the clearance from the RPE plasma membrane homogenous throughout the RPE monolayer?

In the area of AAV infection, the effects are very homogenous. In the uninfected area, the clearance does not occur, and we consider the uninfected area of the same eye to be an excellent internal control.

A statistical analysis (as was provided for other experiments in the manuscript) would help to make the surprising conclusion about C.Txhniip.C247S more convincing.

In this revision, we used the Mann-Whitney U test with the Bonferroni correction for GLUT1 intensity quantification. For the cone survival statistics, we used the t-test or ANOVA with Dunnett multiple comparison test. The information has been added to each figure legend.

Another improvement I suggest for this figure is to include normal full length Txnip as a positive control to show how completely it removes GLUT1 from the surface.

Added. See the new Figure 2-figure supplement 1.

Another point that should be discussed is - when Txnip prevents GLUT1 from reaching the surface does all the GLUT1 get fully degraded within the cell. A brief description of how Txnip influences GLUT1 stability and localization would be helpful.

We are unable to track the fate of the GLUT1 after it is removed, i.e. we do not see definitive intracellular staining. We do not know if this is due to degradation or a hidden epitope.

Minor point

(1) Confusing citation on lines 99-100: "We previously showed that overexpressing the Txnip wt allele in the RPE using an RPE specific promoter, derived from the Best1 gene (Esumi et al. 2009),.." makes it sound like Esumi et al. is the citation for their previous study, which is not correct.

We have amended this to: "We previously showed (Xue et al. 2021) that overexpressing the Txnip wt allele in the RPE using an RPE-specific promoter, derived from the Best1 gene (Esumi et al., 2009), did not improve RP cone survival."

Reviewer #2 (Recommendations For The Authors):

Regarding the manuscript, here are some suggestions that authors can take into consideration for the completeness of the study:

(1) The text references the relationship between α-arrestin and glucose metabolism in cone cells, but fails to provide an explanation for its specific involvement in glucose metabolism. Consequently, readers may struggle to discern the targeted metabolic pathway.

We understand this point from Reviewer, and would love to know more about its mechanism, which is one reason why we undertook the current study. The mechanism(s) by which Txnip affects metabolism remains to be elucidated. To summarize our findings from our previous study, we showed that LDHB, which converts lactate to pyruvate, was required for Txnip-mediated rescue. Addition of the LDHB gene, however, did not boost rescue. We also showed that mitochondrial size and membrane potential were improved, and the Na/K pump function was improved, in Txnip-treated cones. Improved mitochondria were not sufficient, however, as revealed by a PARP-1 KO mouse with improved mitochondria that did not extend cone survival. In addition, using a Txnip mutant that does not remove the glucose transporter, we still saw cone rescue, so this function cannot be required for Txnip-mediated rescue. How does Txnip lead to improved mitochondria and to a reliance on lactate? We do not know.

(2) Although the author conducted an experiment on arrdc14 due to its similarity to Txnip, the lack of clarification on why arrdc4, with a 60% amino acid similarity, did not yield the same effects as Txnip remains unaddressed. Highlighting structural disparities or differences in intracellular signaling pathways could potentially shed light on this incongruity. Subsequently, an additional experiment may be warranted to test the hypothesis regarding the effective component of α-arrestin for cone rescue.

Additional experiments are needed to learn of the relevant differences between Arrdc4 and Txnip, but are beyond the scope of our work at the present. However, we have added a paragraph on newly published data on the function of Arrdc4 in the new Discussion:

“Arrdc4, the most similar α-arrestin protein to Txnip that also has Arrestin N- and C- domains, accelerated RP cone death when transduced by AAV (Figure 1). This observation suggests that Txnip has unique functions that protect RP cones. Recently, Arrdc4 has been proposed to be critical for liver glucagon signaling, which could be negated by insulin (Dagdeviren et al. 2023). The implication of this potential role regarding RP cone survival is unclear, but interestingly, the activation of the insulin/mTORC1 pathway is beneficial to RP cone survival (Punzo et al. 2009; Venkatesh et al. 2015).”

(3) The utilization of distinct mutant Txnip variants to impact RPE, cones, and their combined influence is noted. A comparative table elucidating the impact of cone rescue on these three targets would greatly enhance clarity.

We presented these data in Figure 4 in a table format.

Additionally, the text does not definitively establish whether Txnip.C247S.LL351 and 352AA, as well as Txnip.C247S, indeed manifest discrepancies when exclusively affecting RPE.

We edited a sentence in Results to: “Similar to Best1-wt Txnip (Xue et al., 2021), Best1-Txnip.C247S did not show significant improvement of cone survival, ruling out the C247S mutation alone as promoting the cone survival by Best1-Txnip.C247S.LL351 and 352AA.”

(4) While the text mentions that Txnip stimulates lactate utilization within cones, it remains unclear whether this effect extends to RPE. If applicable, this trait could potentially contribute to its role in cone rescue.

We agree with the Reviewer, and hope to address this question in our next study.

(5) The discussion introduces the notion that one potential mechanism for cone rescue by Txnip.C247S involves facilitating unhindered movement of Thioredoxin for redox processes. To validate this hypothesis and elucidate the mechanics of Txnip's involvement in cone rescue, it may be prudent to conduct further experiments concentrating on the interaction between Txnip and thioredoxin. Alternatively, an experiment aimed at upregulating Thioredoxin expression would be a valuable addition.

We hope to address this question in the future. However, the effect may be more complicated than our simple hypothesis regarding release of Thioredoxin. More than a dozen proteins were found to differentially interact with Txnip vs. Txnip.C247S (Forred et al. 2016).

Reviewer #3 (Recommendations For The Authors):

(1) Glucose transporter 1 is identified as an important mechanism in the protection of cone degeneration. It is unclear why GLut1 is upregulated in retinal cells although the expression of Txnip mutants are specifically in the RPE in Figure 2.

This retinal GLUT1 upregulation was not consistently observed in the treated eyes, so we did not comment on it in the text.

(2) Mutant N. Txnip was mentioned in the discussion that it causes obvious retinal degeneration. The quantification of retinal thickness from Figure 2 will be more rigorous.

Unlike the robust effects of Best1-N.Txnip on RPE GLUT1 level, this negative effect of Best1-N.Txnip on ONL thickness was not consistent. This result does not undermine the other major conclusions. Therefore, we deleted the related sentence of the original text: “This hypothesis is supported by the observation that N.Txnip led to an obvious thinning of the outer nuclear layer of the wt retina, reflecting a loss of photoreceptors”. We did leave in the related finding as follows:

“The N-terminal half of Txnip (1-228aa) might exert harmful effects in the RPE, that negate the beneficial effects from the C-terminal half, suggested by the observation that its removal, in the C-terminal 149-397 allele, led to better cone survival when expressed in the RPE (Figure 2). In cones, the C-terminal half, including the C-terminal IDR tail, may cooperate with the N-terminal half, or negate its negative effects, to benefit RP cone survival. However, the C-terminal half is not sufficient for cone rescue when expressed in cones, as the 149-397 allele did not rescue.”

eLife assessment

This fundamental study advances our understanding of the cell specific treatment of cone photoreceptor degeneration by Txnip. The evidence supporting the conclusions is compelling with rigorous genetic manipulation of Txnip mutations. The work will be of broad interest to vision researchers, cell biologists and biochemists.

Reviewer #1 (Public Review):

Summary:

This is a follow-up study to the authors' previous eLife report about the roles of an alpha-arrestin called protein thioredoxin interacting protein (Txnip) in cone photoreceptors and in the retinal pigment epithelium. The findings are important because they provide new information about the mechanism of glucose and lactate transport to cone photoreceptors and because they may become the basis for therapies for retinal degenerative diseases.

Strengths:

Overall, the study is carefully done and, although the analysis is fairly comprehensive with many different versions of the protein analyzed, it is clearly enough described to follow. Figure 4 greatly facilitated my ability to follow, understand and interpret the study. The authors have appropriately addressed a few concerns about statistical significance and the relationship between their findings and previous studies of the possible roles of Txnip on GLUT1 expression and localization on the surfaces of RPE cells.

Reviewer #2 (Public Review):

The hard work of the authors is much appreciated. With overexpression of a-arrestin Txnip in RPE, cones and the combined respectively, the authors show a potential gene agnostic treatment that can be applied to retinitis pigmentosa. Furthermore, since Txnip is related to multiple intracellular signaling pathway, this study is of value for research in the mechanism of secondary cone dystrophy as well.

There are a few areas in which the article may be improved through further analysis and application of the data, as well as some adjustments that should be made in to clarify specific points in the article.

Strengths

- The follow-up study builds on innovative ground by exploring the impact of TxnipC247S and its combination with HSP90AB1 knockdown on cone survival, offering novel therapeutic pathways.<br /> - Testing of different Txnip deletion mutants provides a nuanced understanding of its functional domains, contributing valuable insights into the mechanism of action in RP treatment.<br /> - The findings regarding GLUT1 clearance and the differential effects of Txnip mutants on cone and RPE cells lay the groundwork for targeted gene therapy in RP.

Weaknesses

- The focus on specific mutants and overexpression systems might overlook broader implications of Txnip interactions and its variants in the wider context of retinal degeneration.<br /> - The study's reliance on cell count and GLUT1 expression as primary outcomes misses an opportunity to include functional assessments of vision or retinal health, which would strengthen the clinical relevance.<br /> - The paper could benefit from a deeper exploration of why certain treatments (like Best1-146 Txnip.C247S) do not lead to cone rescue and the potential for these approaches to exacerbate disease phenotypes through glucose shortages.<br /> - Minor inconsistencies, such as the missing space in text references and the need for clarification on data representation (retinas vs. mice), should be addressed for clarity and accuracy.<br /> - The observation of promoter leakage and potential vector tropism issues raise questions about the specificity and efficiency of the gene delivery system, necessitating further discussion and validation.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Sang et al. proposed a pair of IR60b-expressing pharyngeal neurons in Drosophila use IR25a, IR76b, and IR60b channels to detect high Na+ and limit its consumption. Some of the key findings that support this thesis are: 1) animals that lacked any one of these channels - or with their IR60b-expressing neurons selectively silenced - showed much reduced rejection of high Na+, but restored rejection when these channels were reintroduced back in the IR60b neurons; 2) animals with TRPV artificially expressed in their IR60b neurons rejected capsaicin-laced food whereas WT did not; 3) IR60b-expressing neurons exhibited increased Ca2+ influx in response to high Na+ and such response went away when animals lacked any of the three channels.

Strengths:

The experiments were thorough and well designed. The results are compelling and support the main claim. The development and the use of the DrosoX two-choice assay put forward for a more quantitative and automatic/unbiased assessment for ingestion volume and preference.

Weaknesses:

There are a few inconsistencies with respect the the exact role by which IR60b neurons limit high salt consumption and the contribution of external (labellar) high-salt sensors in regulating high salt consumption. These weaknesses do not significantly impact the main conclusion, however.

Reviewer #2 (Public Review):

Summary:

In this paper, Sang et al. set out to identify gustatory receptors involved in salt taste sensation in Drosophila melanogaster. In a two-choice assay screen of 30 Ir mutants, they identified that Ir60b is required for avoidance of high salt. In addition, they demonstrate that activation of Ir60b neurons is sufficient for gustatory avoidance using either optogenetics or TRPV1 to specifically activate Ir60b neurons. Then, using tip recordings of labellar gustatory sensory neurons and proboscis extension response behavioral assays in Ir60b mutants, the authors demonstrate that Ir60b is dispensable for labellar taste neuron responses to high salt and the suppression of proboscis extension by high salt. Since external gustatory receptor neurons (GRNs) are not implicated, they look at Poxn mutants, which lack external chemosensory sensilla but have intact pharyngeal GRNs. High salt avoidance was reduced in Poxn mutants but was still greater than Ir60b mutants, suggesting that pharyngeal gustatory sensory neurons alone are sufficient for high salt avoidance. The authors use a new behavioral assay to demonstrate that Ir60b mutants ingest a higher volume of sucrose mixed with high salt than control flies do, suggesting that the action of Ir60b is to limit high salt ingestion. Finally, they identify that Ir60b functions within a single pair of gustatory sensory neurons in the pharynx, and that these neurons respond to high salt but not bitter tastants.

Strengths:

A great strength of this paper is that it rigorously corroborates previously published studies that have implicated specific Irs in salt taste sensation. It further introduces a new role for Ir60b in limiting high salt ingestion, demonstrating that Ir60b is necessary and sufficient for high salt avoidance and convincingly tracing the action of Ir60b to a particular subset of gustatory receptor neurons. Overall, the authors have achieved their aim by identifying a new gustatory receptor involved in limiting high salt ingestion. They use rigorous genetic, imaging, and behavioral studies to achieve this aim, often confirming a given conclusion with multiple experimental approaches. They have further done a great service to the field by replicating published studies and corroborating the roles of a number of other Irs in salt taste sensation. An aspect of this study that merits further investigation is how the same gustatory receptor neurons and Ir in the pharynx can be responsible for regulating the ingestion of both appetitive (sugar) and aversive tastants (high salt).

A previous report published in eLife from John Carlson’s lab (Joseph et al, 2017) showed that the Ir60b GRN in the pharynx responds to sucrose resulting in sucrose repulsion. Thus, stimulation of this pharyngeal GRN results in gustatory avoidance only, not both attraction and avoidance. (lines 205-207)

Weaknesses:

There are several weaknesses that, if addressed, could greatly improve this work.

(1) The authors combine the results and discussion but provide a very limited interpretation of their results. More discussion of the results would help to highlight what this paper contributes, how the authors interpret their results, and areas for future study.

We agree and have now separated the Results and Discussion, and in so doing have greatly expanded discussion of the results.

(2) The authors rename previously studied populations of labellar GRNs to arbitrary letters, which makes it difficult to understand the experiments and results in some places. These GRN populations would be better referred to according to the gustatory receptors they are known to express.

One of the corresponding authors (Craig Montell) introduced this alternative GRN nomenclature in a review in 2021: Montell, C. (Drosophila sensory receptors—a set of molecular Swiss Army Knives. Genetics 217, 1-34) (Montell, 2021). We are not fans of referring to different classes of GRNs based on the receptors that they express since it is not obvious which receptors to use. For example, the GRNs that respond to bitter compounds all express multiple GR co-receptors. The same is true for the GRNs that respond to sugars. The former system of referring to GRNs simply as sugar, bitter, salt and water GRNs is also not ideal since the repertoire of chemicals that stimulates each class is complex. For example, the Class A GRNs (formerly sugar GRNs) are also activated by low Na+, glycerol, fatty acids, and acetic acid, while the B GRNs (former bitter GRNs) are also stimulated by high Na+, acids, polyamines, and tryptophan. In addition, there are five classes of GRNs. At first mention of the Class A—E GRNs, we mention the most commonly used former nomenclature of sugar, bitter, salt and water GRNs. In addition, for added clarify, we now also include a mention of one of the receptors that mark each class. (lines 51-59)

(3) The conclusion that GRNs responsible for high salt aversion may be inhibited by those that function in low salt attraction is not well substantiated. This conclusion seems to come from the fact that overexpression of Ir60b in salt attraction and salt aversion sensory neurons still leads to salt aversion, but there need not be any interaction between these two types of sensory neurons if they act oppositely on downstream circuits.

We did not make this claim.

(4) The authors rely heavily on a new Droso-X behavioral apparatus that is not sufficiently described here or in the previous paper the authors cite. This greatly limits the reader's ability to interpret the results.

We expanded the description of the apparatus in the Droso-X assay section of the Materials and Methods. (lines 588-631)

Reviewer #3 (Public Review):

Summary:

Sang et al. successfully demonstrate that a set of single sensory neurons in the pharynx of Drosophila promotes avoidance of food with high salt concentrations, complementing previous findings on Ir7c neurons with an additional internal sensing mechanism. The experiments are well-conducted and presented, convincingly supporting their important findings and extending the understanding of internal sensing mechanisms. However, a few suggestions could enhance the clarity of the work.

Strengths:

The authors convincingly demonstrate the avoidance phenotype using different behavioral assays, thus comprehensively analyzing different aspects of the behavior. The experiments are straightforward and well-contextualized within existing literature.

Weaknesses:

Discussion

While the authors effectively relate their findings to existing literature, expanding the discussion on the surprising role of Ir60b neurons in both sucrose and salt rejection would add depth. Additionally, considering Yang et al. 2021's (https://doi.org/10.1016/j.celrep.2021.109983) result that Ir60b neurons activate feeding-promoting IN1 neurons, the authors should discuss how this aligns with their own findings.

Yang et al. demonstrated that the activation of Ir60b neurons can trigger the activation of IN1 neurons akin to pharyngeal multimodal (PM) neurons, potentially leading to enhanced feeding (Yang et al, 2021). However, our research reveals a specific pattern of activation for Ir60b neurons. Instead of being generalists, they are specialized for certain sugars, such as sucrose and high salt. Consequently, while Ir60b GRNs activate IN1 neurons, we contend that there are other neurons in the brain responsible for inhibiting feeding. (lines 412-417)

Lines 187: The discussion primarily focuses on taste sensillae outside the labellum, neglecting peg-type sensillae on the inner surface. Clarification on whether these pegs contribute to the described behaviors and if the Poxn mutants described also affect the pegs would strengthen the discussion.

We added the following to the Discussion section. “We also found that the requirement for Ir60b appears to be different when performing binary liquid capillary assay (DrosoX), versus solid food binary feeding assays. When we employed the DrosoX assay to test mutants that were missing salt aversive GRNs in labellar bristles but still retained functional Ir60b GRNs, the flies behaved the same as wild-type flies (e.g. Figure 3J and 3L). However, using solid food binary assays, Poxn mutants, which are missing labellar taste bristles but retain Ir60b GRNs (LeDue et al, 2015), displayed repulsion to high salt food that was intermediate between control flies and the Ir60b mutant (Figure 2J). Poxn mutants retain taste pegs (LeDue et al., 2015), and these hairless taste organs become exposed to food only when the labial palps open. We suggest that there are high-salt sensitive GRNs associated with taste pegs, which are accessed when the labellum contacts a solid substrate, but not when flies drink from the capillaries used in DrosoX assays. This explanation would also account for the findings that the Ir60b mutant is indifferent to 300 mM NaCl in the DrosoX assay (Figure 3B), but prefers 1 mM sucrose alone over 300 mM NaCl and 5 mM sucrose in the solid food binary assay (Figure 1B).”. (lines 430-444)

In line 261 the authors state: "We attempted to induce salt activation in the I-type sensilla by ectopically expressing Ir60b, similar to what was observed with Ir56b 8; however, this did not generate a salt receptor (Figures S6A)"

An obvious explanation would be that these neurons are missing the identified necessary co-receptors Ir76b and Ir25a. The authors should discuss here if the Gr33a neurons they target also express these co-receptors, if yes this would strengthen their conclusion that an additional receptor might be missing.

We clarified this point in the Discussion section as follows, “An open question is the subunit composition of the pharyngeal high Na+ receptor, and whether the sucrose/glucose and Na+ receptors in the Ir60b GRN are the same or distinct. Our results indicate that the high salt sensor in the Ir60b GRN includes IR25a, IR60b and IR76b since all three IRs are required in the pharynx for sensing high levels of NaCl. I-type sensilla do not elicit a high salt response, and we were unable to induce salt activation in I-type sensilla by ectopically expressing Ir60b, under control of the Gr33a-GAL4. This indicates that IR25a, IR60b and IR76b are insufficient for sensing high Na+. The inability to confer a salt response by ectopic expression of Ir60b was not due to absence of Ir25a and Ir76b in Gr33a GRNs since Gr33a and Gr66a are co-expressed (Moon et al, 2009), and Gr66a GRNs express Ir25a and Ir76b (Li et al, 2023). Thus, the high salt receptor in Ir60b GRNs appears to require an additional subunit. Given that Na+ and sugars are structurally unrelated, we suggest that the Na+ and sucrose/glucose receptors do not include the identical set of subunits, or that that they activate a common receptor through disparate sites”. (lines 464-477)

Methods

The description of the Droso-X assay seems to be missing some details. Currently, it is not obvious how the two-choice is established. Only one capillary is mentioned, I assume there were two used? Also, the meaning of the variables used in the equation (DrosoX and DrosoXD) are not explained.

We expanded the description of the apparatus in the Droso-X assay section of the Materials and Methods. (lines 588-631)

The description of the ex-vivo calcium imaging prep. is unclear in several points:

(1) It is lacking information on how the stimulus was applied (was it manually washed in? If so how was it removed?).

We expanded the description of the apparatus in the ex vivo calcium imaging section of the Materials and Methods. (lines 682-716)

(2) The authors write: "A mild swallow deep well was prepared for sample fixation." I assume they might have wanted to describe a "shallow well"?

We deleted the word “deep.”.(line 691)

(3) "...followed by excising a small portion of the labellum in the extended proboscis region to facilitate tastant access to pharyngeal organs." It is not clear to me how one would excise a small portion of the labellum, the labellum depicts the most distal part of the proboscis that carries the sensillae and pegs. Did the authors mean to say that they cut a part of the proboscis?

Yes. We changed the sentence to “…followed by excising a small portion of the extended proboscis to facilitate tastant access to the pharyngeal organs.”.(lines 693)-695

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In this manuscript, Sang et al. proposed a pair of IR60b-expressing pharyngeal neurons in Drosophila use IR25a, IR76b, and IR60b channels to detect high Na+ and limit its consumption. Some of the key findings that support this thesis are: 1) animals that lacked any one of these channels - or with their IR60b-expressing neurons selectively silenced - showed much reduced rejection of high Na+, but restored rejection when these channels were reintroduced back in the IR60b neurons; 2) animals with TRPV artificially expressed in their IR60b neurons rejected capsaicin-laced food whereas WT did not; 3) IR60b-expressing neurons exhibited increased Ca2+ influx in response to high Na+ and such response went away when animals lacked any of the three channels. In general, I find the collective evidence presented by the authors convincing. But I feel the MS can benefit from having a discussion session and a few simple experiments. Below I listed some inconsistencies I hope the authors can address or at least discuss.

We have now added a Discussion section, and expanded the discussion.

(1) The role of IR60b neurons on suppressing PER appeared inconsistent. On the one hand, optogenetic activation of these neurons suppressed PER (Fig 1D), on the other hand, IR60b mutants were as competent to suppress PER in response to high salt as WT (Fig 2G). Are pharyngeal neurons expected to modulate PER? It might be worth including a retinal-free or genotype control to ascertain the PER suppression exhibited by IR60b>CsChrimson is genuine.

Please note that Figure 2G is now Figure 2H.

Our interpretation is that activation of aversive GRNs by high salt either in labellar bristles or in the pharynx is sufficient to inhibit repulsion to high salt. Consistent with this conclusion, optogenetic activation of Ir60b GRNs, which are specific to the pharynx, is sufficient to reduce the PER to sucrose containing food (Figure 1D). However, mutation of Ir60b has no impact on the PER to sucrose plus high (300 mM) NaCl since the high-salt activated GRNs in labellar bristles are not impaired by the Ir60b mutation. In contrast, Ir25a and Ir76b are required in both labellar bristles and in the pharynx to reject high salt. As a consequence, mutation of either Ir25a or Ir76b impairs the repulsion to high salt. Thus, there is no inconsistency between the optogenetics and PER results. We clarified this point in the Discussion section. In terms of controls for IR60b>CsChrimson, we show that UAS-CsChrimson alone or UAS-CsChrimson in combination with the Gr5a driver has no impact on the PER (Figure 1D). In addition, we now include a retinal free control (Figure 1D). These findings provide the key genetic controls and are described in the Results section. (lines 167-170)

(2) The role of labellar high-salt sensors in regulating salt intake appeared inconsistent. On the one hand, they appeared to have a role in limiting high salt consumption because poxn mutants were significantly more receptive to high salt than WT (Fig. 2J). On the other hand, selectively restoring IR76b or IR25a in only the IR60b neurons in these mutants - thus leaving the labellar salt sensors still defective - reverted the flies to behave like WT when given a choice between sucrose vs. sucrose+high salt (Fig 3J, L).

We now offer an explanation for these seemingly conflicting results in the Discussion section. When we employed the DrosoX assay with mutants with functional Ir60b GRNs, but were missing salt aversive GRNs in labellar bristles, the flies behaved the same as control flies (e.g. Figure 3J and L). However, using solid food binary assays, Poxn mutants, which are missing labellar taste bristles but retain Ir60b GRNs (LeDue et al., 2015), display aversion high salt food intermediate between control and Ir60b mutant flies (Figure 2J). Poxn mutants retain taste pegs (LeDue et al., 2015), which are exposed to food substrates only when the labial palps open. We suggest that the taste pegs harbor high salt sensitive GRNs, and they may be exposed to solid substrates, but not to the liquid in capillary tubes used in the DrosoX assays. This explanation would also account for the findings that the Ir60b mutant is indifferent to 300 mM NaCl in the DrosoX assay (Figure 3B), but prefers 1 mM sucrose alone over 300 mM NaCl and 5 mM sucrose in the solid food binary assay (Figure 1B). (lines 433-444)

(3) The behavior sensitivity of IR60b mutant to high salt again appeared somewhat inconsistent when assessed in the two different choice assays. IR60b mutant flies were indifferent to 300 mM NaCl when assayed with DrosoX (Fig 3A, B) but were clearly still sensitive to 300 mM NaCl when assayed with "regular" assay - they showed much reduced preference for 5 mM sucrose over 1 mM sucrose when the 5 mM sucrose was adulterated with 300 mM NaCl (Fig 1B).

The explanation provided above may also account for the findings that the Ir60b mutant is indifferent to 300 mM NaCl in the DrosoX assay (Figure 3B), but not when selecting between 300 mM NaCl and 5 mM sucrose versus 1 mM sucrose in the solid food binary assay (Figure 1B). Alternatively, the different behavioral responses might be due to the variation in sucrose concentrations in each of these two assays, which employed 5 mM sucrose in the solid food binary assay, as opposed to 100 mM sucrose in the DrosoX assay. This disparity in attractive valence between these two concentrations of sucrose might consequently impact feeding amount and preference. This point is now also included in the Discussion section. (lines 441-449)

(4) Given the IR60b neurons exhibited clear IR60b/IR25a/IR76b-dependent sucrose sensitivity, too, I am curious how the various mutant animals behave when given a choice between 100 mM sorbitol vs. 100 mM sorbitol + 300 mM NaCl, a food choice assay not complicated by the presence of sucrose. Similarly, I am curious if the Ca2+ response of IR60 neurons differs significantly when presented with 100 mM sucrose vs. when presented with 100 mM sucrose + 300 mM NaCl. In principle, the magnitude for the latter should be significantly larger than the former as animals appeared to be capable of discriminating these two choices solely relying on their IR60b neurons.

To investigate the aversion induced by high salt in the absence of a highly attractive sugar, such as sucrose, we combined 300 mM salt with 100 mM sorbitol, which is a tasteless but nutritive sugar (Burke & Waddell, 2011; Fujita & Tanimura, 2011). Using two-way choice assays, we found that the Ir25a, Ir60b, and Ir76b mutants exhibited substantial reductions in high salt avoidance (Figure 3—figure supplement 2A). In addition, we performed DrosoX assays using 100 mM sorbitol alone, or sorbitol mixed with 300 mM NaCl. Sorbitol alone provoked less feeding than sucrose since it is a tasteless sugar (Figure 3—figure supplement 2B and C). Nevertheless, addition of high salt to the sorbitol reduced food consumption (Figure 3—figure supplement 2B and C). (lines 300-308)

We also conducted a comparative analysis of the Ca2+ responses within the Ir60b GRN, examining its reaction to various stimuli, including 100 mM sucrose alone, 300 mM NaCl alone, and a combination of 100 mM sucrose and 300 mM NaCl. We found that the Ca2+ responses were significantly higher when we exposed the Ir60b GRN to 300 mM NaCl alone, compared with the response to 100 mM sucrose alone (Figure 4—figure supplement 1D). However, the GCaMP6f responses was not higher when we presented 100 mM sucrose with 300 mM NaCl, compared with the response to 300 mM NaCl alone (Figure 4—figure supplement 1D). (lines 360-367)

Minor issues

(1) The labels of sucrose concentration on Figure 2D were flipped.

This has been corrected.

(2) The phrasing of the sentence that begins in line 196 (i.e., "This suggests the internal sensor ...") is not as optimal.

We changed the sentence to, “We found that the aversive behavior to high salt was reduced in the Poxn mutants relative to the control (Figure 2J), consistent with previous studies demonstrating roles for GRNs in labellar bristles in high salt avoidance (Jaeger et al, 2018; McDowell et al, 2022; Zhang et al, 2013).”. (lines 217-219)

(3) In Line 231, I am not sure why the authors think ectopic expressing IR60b in labellar neurons would allow them to become activated by Na+. It seems highly unlikely to me, especially given IR60b also plays a role in sensing sugar.

We added the following paragraph to the Discussion addressing this point, “An open question is the subunit composition of the pharyngeal high Na+ receptor, and whether the sucrose/glucose and Na+ receptors in the Ir60b GRN are the same or distinct. Our results indicate that the high salt sensor in the Ir60b GRN includes IR25a, IR60b and IR76b since all three IRs are required in the pharynx for sensing high levels of NaCl. I-type sensilla do not elicit a high salt response, and we were unable to induce salt activation in I-type sensilla by ectopically expressing Ir60b, under control of the Gr33a-GAL4. This indicates that IR25a, IR60b and IR76b are insufficient for sensing high Na+. The inability to confer a salt response by ectopic expression of Ir60b was not due to absence of Ir25a and Ir76b in Gr33a GRNs since Gr33a and Gr66a are co-expressed (Moon et al., 2009), and Gr66a GRNs express Ir25a and Ir76b (Li et al., 2023). Thus, the high salt receptor in Ir60b GRNs appears to require an additional subunit. Given that Na+ and sugars are structurally unrelated, we suggest that the Na+ and sucrose/glucose receptors do not include the identical set of subunits, or that that they activate a common receptor through disparate sites.”. (lines 464-477)

Reviewer #2 (Recommendations For The Authors):

Line 41, acutely excessive salt ingestion can lead to death, not just health issues

We now state that, “consumption of excessive salt can contribute to various health issues in mammals, including hypertension, osteoporosis, gastrointestinal cancer, autoimmune diseases, and can lead to death.”. (lines 41-43)

Line 46, delete the comma after flies

Done. (line 47)

Lines 51-56: This description is unnecessarily confusing and does not cite proper sources. Renaming these GRNs arbitrarily can only create confusion, plus this description lacks nuance. If E GRNs are Ir94e positive, this description is out of date. Furthermore, If D GRNs are ppk23 and Gr66a positive then they will respond to both bitter and high salt.

Papers to consult: https://elifesciences.org/articles/37167 10.1016/j.cell.2023.04.038

We have now added citations. We prefer the A—E nomenclature, which was introduced in a 2021 Genetics review by one of the authors of this manuscript (Montell) (Montell, 2021) since naming different classes of GRNs on the basis of markers or as sweet, bitter, salt and water GRNs is misleading and an oversimplification. We cite the Genetics 2021 review, and for added clarity include both types of former names (markers and sweet, bitter, salt and water). Class D GRNs are not marked by Gr66a. The eLife reference cited above provided the initial rationale for stating that Class E GRNs are marked by Ir94e and activated by low salt. According to the Taisz et al reference (Cell 2023), the Class E GRNs, which are marked by Ir94e, are also activated by pheromones, which we now mention (Taisz et al, 2023). (lines 51-59)

Line 62, E GRNs are not required for low salt behaviors

We do not state that E GRNs are required for low salt behaviors, only that they sense low Na+ levels. (line 58)

Line 70-81 - Great deal of emphasis on labellar GRNs but then no mention of how pharyngeal GRNs fit into categories A-E

We devote the following paragraph to pharyngeal GRNs. We do not mention how they fit in with the A—E categories because it is not clear.

“In addition to the labellum and taste bristles on other external structures, such as the tarsi, fruit flies are endowed with hairless sensilla on the surface of the labellum (taste pegs), and three internal taste organs lining the pharynx, the labral sense organ (LSO), the ventral cibarial sense organ (VCSO), and the dorsal cibarial sense organ (DCSO), which also function in the decision to keep feeding or reject a food (Chen & Dahanukar, 2017, 2020; LeDue et al., 2015; Nayak & Singh, 1983; Stocker, 1994). A pair of GRNs in the LSO express a member of the gustatory receptor family, Gr2a, and knockdown of Gr2a in these GRNs impairs the avoidance to slightly aversive levels of Na+ (Kim et al, 2017). Pharyngeal GRNs also promote the aversion to bitter tastants, Cu2+, L-canavanine, and bacterial lipopolysaccharides (Choi et al, 2016; Joseph et al., 2017; Soldano et al, 2016; Xiao et al, 2022). Other pharyngeal GRNs are stimulated by sugars and contribute to sugar consumption (Chen & Dahanukar, 2017; Chen et al, 2021; LeDue et al., 2015). Remarkably, a pharyngeal GRN in each of the two LSOs functions in the rejection rather the acceptance of sucrose (Joseph et al., 2017).”. (lines 74-89)

Line 89, aversive --> aversion

We changed this part.

Line 90, gain of aversion capsaicin avoidance suggests they are sufficient for avoidance, not essential for avoidance.

We changed “essential” to “sufficient.”. (line 100)

Line 104, what are you recording from here? Labellar or pharyngeal GRNs

We added “S-type and L-type sensilla” to the sentence. (line 119)

Line 107, How are A GRNS marked with tdTomato? It is important to mention how you are defining A GRNs.

We modified the sentence as follows: “Using Ir56b-GAL4 to drive UAS-mCD8::GFP, we also confirmed that the reporter was restricted to a subset of Class A GRNs, which were marked with LexAop-tdTomato expressed under the control of the Gr64f-LexA (Figure 1—figure supplement 1D—F).”. (lines 120-123)

Line 124, should read "concentrated as sea water."

We made the change. (line 142)

Line 125, I am not sure what is meant by "alarm neurons"

We changed “additional pain or alarm neurons” to “nociceptive neurons.”. (line 144)

Line 141, Are you definitely A GRNs as only labellar GRNs, i.e. the Gr5a-GAL4 pattern with labellar plus few pharyngeal GRNs? Or are the defining it as Gr64f-GAL4 (i.e. labellar plus many pharyngeal GRNs)

We refer to the Class A—E GRNs as labellar GRNs. Therefore, in this instance, we removed the reference to A GRNs and B GRNs, and simply mention the drivers that we used (Gr5a-GAL4 and Gr66a-GAL4) to express UAS-CsChrimson. The modified sentence is, “As controls we drove UAS-CsChrimson under control of either the Gr5a-GAL4 or the Gr66a-GAL4.”. (lines 51-59, 160-161)

Line 180, labellar hairs--> labellar taste bristles

We made the change. (line 204)

Line 190, possess only --> only possess

We made the change. (line 216)

Line 202, Should this read increased?

Yes. We changed “reduced” to “increased.”. (line 225)

Line 206, The information provided here and in reference 47 was not sufficient for me to understand how the Droso-X system works and whether it has been validated. Better diagrams and much more description is required for the reader to understand this system and assess its validity

We now explain that the DrosoX “system consists of a set of five separately housed flies, each of which is exposed to two capillary tubes with different liquid food options. One capillary contained 100 mM sucrose and the other contained 100 mM sucrose mixed with 300 mM NaCl. The volume of food consumed from each capillary is then monitored automatically over the course of 6 hours and recorded on a computer.”. (lines 238-243)

Line 218-219, It would be helpful to expand on this to explain how the previous paper detected no difference. Is this because the contact time with the food is the same but the rate of ingestion is slower?

Yes. This is correct. We now clarify this point by stating that, “In a prior study, it was observed that the repulsion to high salt exhibited by the Ir60b mutant was indistinguishable from wild-type (Joseph et al., 2017). Specifically, the flies were presented with drop of liquid (sucrose plus salt) at the end of a probe, and the Ir60b mutant flies fed on the food for the same period of time as control flies (Joseph et al., 2017). However, this assay did not discern whether or not the volume of the high salt-containing food consumed by the Ir60b mutant flies was reduced relative to control flies. Therefore, to assess the volume of food ingested, we used the DrosoX system, which we recently developed (Figure 3—figure supplement 1A) (Sang et al, 2021). This system consists of a set of five separately housed flies, each of which is exposed to two capillary tubes with different liquid food options. One capillary contained 100 mM sucrose and the other contained 100 mM sucrose mixed with 300 mM NaCl. The volume of food consumed from each capillary was then monitored automatically over the course of 6 hours and recorded on a computer. We found that control flies consuming approximately four times more of the 100 mM sucrose than the sucrose mixed with 300 mM NaCl (Figure 3A). In contrast, the Ir25a, Ir60b, and Ir76b mutants consumed approximately two-fold less of the sucrose plus salt (Figure 3A). Consequently, they ingested similar amounts of the two food options (Figure 3B; ingestion index). Thus, while the Ir60b mutant and control flies spend similar amounts of time in contact with high salt-containing food when it is the only option (Joseph et al., 2017), the mutant consumes considerably less of the high salt food when presented with a sucrose option without salt.”. (lines 226-251)

Lines 231-235, Is this evidence for this, that Ir60b expression in the Ir25a or Ir76b pattern will induce high salt responses in the labellum? You should elaborate on this to clearly state what you mean rather than implying it. I do not think that overexpression of one Ir is enough evidence for this sweeping conclusion.

We agree. We eliminated this point. (lines 227-232)

Lines 261-263, Please elaborate here, how did you target the I-type sensilla and where are these neurons? So they already express Ir76b and Ir25a?

We now explain in the Results that, “We attempted to induce salt activation in the I-type sensilla by ectopically expressing Ir60b, under control of the Gr33a-GAL4. Gr33a is co-expressed with Gr66a (Moon et al., 2009), which has been shown to be co-expressed Ir25a and Ir76b (Li et al., 2023). When we performed tip recordings from I7 and I10 sensilla, we did not observe a significant increase in action potentials in response to 300 mM NaCl (Figure 4—figure supplement 1A), indicating that ectopic expression of Ir60b in combination with Ir25a and Ir76b is not sufficient to generate a high salt receptor.”. (lines 324-330)

Lines 300-303, The discussion needs to be greatly expanded. What is the proposed mechanism by which the same neurons/receptors can inhibit sucrose and high salt feeding? What is the author's interpretation of what this study adds to our understanding of taste aversion?

We have now added a Discussion section and greatly expanded the discussion.

Reviewer #3 (Recommendations For The Authors):

In line 73 there is a typo in "esophagus"

We changed this part.

In line 331, the use of a mixture of sucrose and "saponin" seems to be a mistake; "NaCl" is likely intended.

We made the correction. (lines 546 and 640)

On several occasions, the authors refer to the pharynx as a taste organ (for example 1st sentence of the abstract). I am not sure this is correct, the actual pharyngeal taste organs are the LSO, DSCO, and VSCO which are located in the pharynx.

We made the corrections. (lines 24, 90, 92, 93, and 356)

In line 155 the authors refer to Ir25a and Ir76b as "broadly tuned". I think it is not correct to refer to co-receptors this way, I'd suggest to just call them co-receptors.

We made the correction. (lines 177-178)

In line 182, stating "Gr2a is also expressed in the proboscis" is unclear. Clarify whether it refers to sensillae, pharyngeal taste organs, etc.

We clarified it refers to pharyngeal taste organs. (lines 206-207)

Line 253: "These finding imply that all three Irs are coexpressed in the pharynx." "The pharynx" is very unspecific, did the authors mean to say "the same neuron"?

We now clarify by saying “in the Ir60b GRN in the pharynx.”. (line 317)

Figures & Legends

I found it confusing that the same color scale is being reused for different panels with different meanings repeatedly and in inconsistent ways. For example in Figure 2, red and blue are being used for Ir25a² mutants, while blue is also being used for Gr64f-Gal4 and S type sensilla. It is also not easily visible nor mentioned in the caption which of the 3 color scales presented belong to which panels.

We modified the colors in the figures so that they are used in a consistent way. We now also define the colors in the legends.

In Figure 2 F-I, indicating the stimulus sequence in each panel would enhance clarity. The color scale in Figure 3 could benefit from explicit explanations of different shades in the caption for easier interpretation.

For example: "The ingestion of (a, dark color) 100 mM sucrose alone and (b, light color) in combination with 300 mM"

We made the suggested modification.

In Figure 4a the authors highlight that Ir76b and Ir25a label 2 neurons in the LSO. Did the imaging in 4c also capture the second cell, and if so did it respond to their stimulation?

No, the focal plane differs, and the signal in Figure 4C is considerably weaker compared to the immunohistochemistry shown in Figure 4A. Notably, the other neuron did not exhibit a response to NaCl.

In Figure 4f a legend for the color scale is missing, or the color might not be necessary at all. Also, the asterisks seem to be shifted to the right.

We fixed the shifted asterisks and eliminated the color.

Figure 4i is mislabeled 4f

We made the correction.

eLife assessment

This valuable study on the molecular and cellular mechanisms of ingestion avoidance of high salt in insects is focused in scope, but the authors present convincing evidence that a specific subset of gustatory receptors in a pair of pharyngeal taste neurons are necessary and sufficient for avoiding ingestion of high salt during feeding. This work will be of interest to Drosophila neuroscientists interested in taste coding and feeding behavior.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Sang et al. proposed a pair of IR60b-expressing pharyngeal neurons in Drosophila use IR25a, IR76b, and IR60b channels to detect high Na+ and limit its consumption. Some of the key findings that support this thesis are: 1) animals that lacked any one of these channels - or with their IR60b-expressing neurons selectively silenced - showed much reduced rejection of high Na+, but restored rejection when these channels were reintroduced back in the IR60b neurons; 2) animals with TRPV artificially expressed in their IR60b neurons rejected capsaicin-laced food whereas WT did not; 3) IR60b-expressing neurons exhibited increased Ca2+ influx in response to high Na+ and such response went away when animals lacked any of the three channels.

The experiments were thorough and well designed and further improved after revision. The results are compelling and support the main claim. The development and the use of the DrosoX two-choice assay put forward for a more quantitative and automatic/unbiased assessment for ingestion volume and preference.

Reviewer #2 (Public Review):

Summary:

In this paper, Sang et al. set out to identify gustatory receptors involved in salt taste sensation in Drosophila melanogaster. In a two-choice assay screen of 30 Ir mutants, they identify that Ir60b is required for avoidance of high salt. In addition, they demonstrate that activation of Ir60b neurons is sufficient for gustatory avoidance using either optogenetics or TRPV1 to specifically activate Ir60b neurons. Then, using tip recordings of labellar gustatory sensory neurons and proboscis extension response behavioral assays in Ir60b mutants, the authors demonstrate that Ir60b is dispensable for labellar taste neuron responses to high salt and the suppression of proboscis extension by high salt. Since external gustatory receptor neurons (GRNs) are not implicated, they look at Poxn mutants, which lack external chemosensory sensilla but have intact pharyngeal GRNs. High salt avoidance was reduced in Poxn mutants but was still greater than Ir60b mutants, suggesting that pharyngeal gustatory sensory neurons alone are sufficient for high salt avoidance. The authors use a new behavioral assay to demonstrate that Ir60b mutants ingest a higher volume of sucrose mixed with high salt than control flies do, suggesting that the action of Ir60b is to limit high salt ingestion. Finally, they identify that Ir60b functions within a single pair of gustatory sensory neurons in the pharynx, and that these neurons respond to high salt but not bitter tastants.

Strengths:

A great strength of this paper is that it rigorously corroborates previously published studies that have implicated specific Irs in salt taste sensation. It further introduces a new role for Ir60b in limiting high salt ingestion, demonstrating that Ir60b is necessary and sufficient for high salt avoidance and convincingly tracing the action of Ir60b to a particular subset of gustatory receptor neurons. Overall the authors have achieved their aim by identifying a new gustatory receptor involved in limiting high salt ingestion. They use rigorous genetic, imaging, and behavioral studies to achieve this aim, often confirming a given conclusion with multiple experimental approaches. They have further done a great service to the field by replicating published studies and corroborating the roles of a number of other Irs in salt taste sensation.

Reviewer #3 (Public Review):

Sang et al. successfully demonstrate that a set of single sensory neurons in the pharynx of Drosophila promotes avoidance of food with high salt concentrations, complementing previous findings on Ir7c neurons with an additional internal sensing mechanism. The experiments are well-conducted and presented, convincingly supporting their important findings and extending the understanding of internal sensing mechanisms.

The authors convincingly demonstrate the avoidance phenotype using different behavioral assays, thus comprehensively analyzing different aspects of the behavior. The experiments are straightforward and well-contextualized within existing literature.

Author Response

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

This study highlights new insights into the mechanism of pheochromocytoma pathogenesis that remains poorly understood. In the context of hereditary syndromes, such as multiple endocrine neoplasia 2 (MEN-2), where RET mutation is the major driver of thyroid, parathyroid, and adrenal pathologies, including pheochromocytoma, this mechanistic dissection of RET and TMEM127 is fundamentally sound. While the significance was deemed important, the strength of the evidence was found to be solid,

Recognizing the limitations of models available for study of neuroendocrine cancers, and specifically for pheochromocytomas, we have revised and clarified the text of the current manuscript version and provide specific responses to the additional comments provided below, highlighting changes and new data.

Reviewer #1 (Recommendations For The Authors):

A current lack of pheochromocytoma cell lines and the use of generated cell lines for mechanistic studies presents a significant challenge that may undermine the inferred value of these findings in mock in vitro systems and question reproducibility in pheochromocytoma. Consideration for 3-dimensional patient-derived pheochromocytoma organoid in vitro and patient-derived organoid xenograft in vivo models will enable confirmation or refute novel findings described by the authors.

We agree completely with Reviewer 1 that ideally, we should replicate these findings with PCC-derived cells in vitro and in organoids. Despite many attempts, PCC cell lines have proved a major challenge for the field of neuroendocrine cancers. Cell line models are not available and PDOs have proven poorly growing and resistant to manipulations, such as CRISPR KOs or siRNA KD. In studies completed since the submission and review of the present manuscript, and subsequently published elsewhere, we have shown that RET protein is highly expressed in TMEM127-mutant PCC by immunohistochemistry. We also showed that the TMEM127-KO SH-SY5Y cell model does grow more robustly than Mock-KO cells in nude mice and that RET inhibition (Selpercatinib) does lead to tumor regression (Guo et al., 2023), suggesting that our findings may be reproducible in vivo. These findings, and potential caveats of the cell models used have been further discussed in the text.

Reviewer #2 (Recommendations For The Authors):

Most notably, all experiments are conducted in an isogenic single-cell line. This exposes the whole story to be potentially confounded by unknown variables.

In addition, studies would benefit from the adding back of TMEM127, or other methods to modulate endosome and plasma membrane dynamics to mechanistically secure the cause of the findings.

As suggested by Reviewer 2, we have generated a TMEM127 KO in HEK293, an unrelated cell line which expressed low levels of TMEM127 but does not express RET. Consistent with our findings in SH-SY5Y, we saw increased membrane accumulation of endogenous membrane proteins N-cadherin and transferrin receptor-1 in these cells in the absence of TMEM127. Additionally, re-expression of a wildtype TMEM127 (FLAG-TMEM127) in these cells led to dramatic decreases in membrane localization of these proteins (Supplemental Figure 1D). These data suggest that membrane accumulation is indeed TMEM127 dependent, and that these processes are not directly dependent on RET expression.

References

Guo, Q., Z.M. Cheng, H. Gonzalez-Cantu, M. Rotondi, G. Huelgas-Morales, P. Ethiraj, Z. Qiu, J. Lefkowitz, W. Song, B.N. Landry, H. Lopez, C.M. Estrada-Zuniga, S. Goyal, M.A. Khan, T.J. Walker, E. Wang, F. Li, Y. Ding, L.M. Mulligan, R.C.T. Aguiar, and P.L.M. Dahia. 2023. TMEM127 suppresses tumor development by promoting RET ubiquitination, positioning, and degradation. Cell Rep. 42:113070.

eLife assessment

This valuable paper provides convincing evidence that loss of the tumor suppressor TMEM127 causes disorganization of plasma membrane lipid domains, alters clathrin assembly, and inhibits endocytosis of a variety of cell surface receptors, leading to increased cell surface levels of signaling proteins including RET and other transmembrane receptor tyrosine kinases. The results are significant for understanding how RET127 loss contributes to pheochromocytoma, although the evidence is indirect owing to the lack of human pheochromocytoma cell lines. The results will be of interest for researchers studying pheochromocytoma and endocytosis mechanisms.

Reviewer #4 (Public Review):

Summary:

Walker et al. investigated the function of TMEM127 on RET regulation and function that could contribute to the development of pheochromocytoma (PCC). The authors showed that deletion of TMEM127 causes RET protein accumulation on the cell surface and, thereby, increased its constitutive ligand-independent activity and downstream signaling. They also unveiled the mechanism of how TMEM127 regulates cell membrane dynamics, particularly focusing on clathrin distribution and its effects on cargo internalization.

Strengths:

They showed that the deletion of TMEM127 affected multiple classes of transmembrane proteins, including RTKs (RET, EGFR), cell adhesion molecules (N-Cadherin, Integrin Beta-3), and carrier proteins (Transferrin Receptor-1), suggesting a global effect on cell surface proteins. This, at least in part, may explain how TMEM127 mutations act as drivers in PCC as well as in other cancers, such as renal cell carcinoma, where RET is not highly expressed. Overall, these findings provide new insights into the understanding of pheochromocytoma pathogenesis and potentially other cancers.

Weaknesses:

The major weakness of this study is the lack of human PCC cell lines for evaluating the function of TMEM127. Currently, the cell line models for pheochromocytoma are unavailable, and manipulation of patient-derived organoids is challenging. To complement this weakness, they provided immunohistochemical data showing that RET protein is highly expressed in TMEM127-mutant PCC.

Furthermore, some of the authors in this manuscript recently published a paper titled 'TMEM127 suppresses tumor development by promoting RET ubiquitination, positioning, and degradation' (Guo et al. Cell Reports 42, 113070, 2023, which is also cited in the current manuscript). In this manuscript, they showed that TMEM127 binds to RET and recruits the NEDD4 E3 ubiquitin ligase for RET ubiquitination and degradation via TMEM127. In general, the ubiquitination of proteins is highly specific to each molecule. In the current version of the manuscript, there is no description of the relevance between these two potentially different mechanisms (clathrin-mediated or ubiquitin-mediated) of accumulating RET and/or other proteins mentioned in two separate papers. I believe the authors should at least discuss this.

Reviewer #5 (Public Review):

Summary:

The manuscript by Walker et al., nicely demonstrated a role of TMEM127 in regulating membrane dynamics of RET, a receptor tyrosine kinase and oncogene for multiple cancers, particularly in pheochromocytoma (PCC). They provided compelling cellular and biochemical evidence on how TMEM127 deficiency reduces RET internalization and degradation in specific cancer cell lines, thus stabilizing cell surface RET and promoting its signaling related to cell proliferation. Moreover, TMEM127 may have a broad function beyond RET, and may affect other surface protein activity such as EGFR etc. These findings provided novel mechanisms and key insights to the field of cancer biology.

Strengths:

Very interesting findings that nicely explained the mechanistic link between TMEM127 and tumorigenesis by RET regulation...the biochemical analysis was quite thorough and impressive.... the general messages delivered by this study are considered as important to the field of TMEM127 biology and tumorigenesis.

Weaknesses:

As acknowledged by the authors, the role of TMEM127 can be conditional and beyond RET modulation, the authors may need to include more discussion that why the loss of TMEM127 is more linked to the development of PCC compared to other cancer types, and why TMEM127 can have such a broad effects in those membrane molecules...in addition, TMEM127 deficiency has been recently linked to enhanced MHC-I-mediated tumor immunity and tumor eradication, in some cancer types...it is then worthwhile to discuss the dual effects of TMEM127 in tumor control in the context of immunity...<br /> Moreover, the authors may need to tune down their "ligand independent" claim on the loss of TMEM127 in driving RET signaling, which should be more related to the level of RET expression/strength of clustering...

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript by DeHaro-Arbona et al., the authors wish to understand how a signaling pathway (Notch) is dynamically decoded to elicit a specific transcriptional output. In particular, they investigate the kinetic properties of Notch-responsive nuclear complexes (the DNA binding factor CSL and its co-activator Mastermind (mam) along with several candidate interacting partners). Their experimental model is the polytene chromosome of the Drosophila salivary gland, in which the naturally inactive Notch can be artificially induced through the expression of a constitutively active form of Notch.

The authors develop a series of CRISPR and transgenic lines enabling the live imaging of these complexes at a specific locus and in various backgrounds (genetic perturbations/drug treatments). This quantitative live imaging data suggests that Notch nuclear complexes form hubs, and the authors characterize their binding dynamics. Interestingly, they elegantly demonstrate that the content of these hubs and their kinetic properties can evolve, even within Notch ON cells. Hence, they propose the existence of distinct hubs, distinguishing an open (CSL), engaged (CSK-Mam), or active (CSL-Mam-Med-PolII) configuration in Notch ON cells and an inactive hub (in Notch OFF having previously been exposed to Notch) state, that would explain the surprising transcriptional memory that the authors observe hours after Notch withdrawal.

We thank the reviewer for this constructive summary of our work

Reviewer #2 (Public Review):

The manuscript from deHaro-Arbona et al, entitled "Dynamic modes of Notch transcription hubs conferring memory and stochastic activation revealed by live imaging the co-activator Mastermind", uses single molecule microscopy imaging in live tissues to understand the dynamics and molecular determinants of transcription factor recruitment to the E(spl)-C locus in Drosophila salivary gland cells under Notch-ON and -OFF conditions. Previous studies have identified the major players that are involved in transcription regulation in the Notch pathway, as well as the importance of general transcriptional coregulators, such as CBP/P300 and the Mediator CDK module, but the detailed steps and dynamics involved in these processes are poorly defined. The authors present a wealth of single molecule data that provides significant insights into Notch pathway activation, including:

(1) Activation complexes, containing CSL and Mam, have slower dynamics than the repressor complexes, containing CSL and Hairless.

(2) Contribution of CSL, NICD, and Mam IDRs to recruitment.

(3) CSL-Mam slow-diffusing complexes are recruited and form a hub of high protein concentrations around the target locus in Notch-ON conditions.

(4) Mam recruitment is not dependent on transcription initiation or RNA production.

(5) CBP/P300 or its associated HAT activity is not required for Mam recruitment.

(6) Mediator CDK module and CDK8 activity are required for Mam recruitment, and vice-versa, but not CSL recruitment.

(7) Mam is not required for chromatin accessibility but is dependent on CSL and NICD.

(8) CSL recruitment and increased chromatin accessibility persist after NICD removal and loss of Mam, which confers a memory state that enables rapid re-activation in response to subsequent Notch activation.

(9) Differences in the proportions of nuclei with both Pol II and with Mam enrichment, which results in transcription being probabilistic/stochastic. These data demonstrate that the presence of Mamcomplexes is not sufficient to drive all the steps required for transcription in every Notch-ON nucleus.

(10) The switch from more stochastic to robust transcription initiation was elicited when ecdysone was added.

Overall, the manuscript is well written, concise, and clear, and makes significant contributions to the Notch field, which are also important for a general understanding of transcription factor regulation and behavior in the nucleus. I recommend that the authors address my relatively minor criticisms detailed below.

We thank the reviewer for their thorough and constructive summary of our work. We are glad that they overall found it insightful and interesting. Below we have addressed the points they have raised.

Page 7, bottom. The authors speculate, "It is possible therefore that, once recruited, Mam can be retained at target loci independently of CSL by interactions with other factors so that it resides for longer." Is it possible that another interpretation of that data is that Mam is a limiting factor?

As indicated our comment is a speculation and is based on the observations summarized in the paragraph. We are not entirely sure what the reviewer is proposing as an alternate model. However, if it relates to the relative concentrations of the different factors, this would not account for the differences in trajectory durations. And for most aspects of our analysis, K[off] has the most profound influence on the results. Furthermore, differences persist even when CSL levels are considerably reduced (as in conditions with Hairless RNAi).

Page 9. The authors write, "A very low level of enrichment was evident for... for the CSL Cterminus..". The recruitment of CSL ct IDR does not appear to be statistically significant or there is no apparent difference (Figure S2C), suggesting the CSL ct IDR does not play a role in enrichment.

We agree with the comments of the reviewer and have adjusted the text on page 9 accordingly.

Page 9. The authors write, "Notably, MamnIDR::GFP fusion was present in droplets, suggesting it can self-associate when present in a high local concentration (Figure S2B)." Is this result only valid for Mam nIDR or does full-length Mam also localize into droplets, as has been previously observed for full-length mammalian Maml1 in transfected cells?

We agree that the observed foci of MamL1 that have been detected in mammalian cells are interesting. We have not tried to replicate those data because the large size of Mam has made it challenging to produce a full-length form in over-expression. We note however that another portion of Mam, MamIDR, does not make droplets when over-expressed despite it containing a large section of the disordered region of the Drosophila Mam. We have now included a comment about the mammalian data in the text (page 9) to put our findings in context.

Previous studies in mammalian cells suggest that Maml1 is a high-confidence target for phosphorylation by CDK8, see Poss et al 2016 Cell Reports https://doi.org/10.1016/j.celrep.2016.03.030. By sequence comparison, does fly Mam have similar potential phosphorylation sites, and might these be critical for Mam/CDK module recruitment?

We thank the reviewer for highlighting this point. Indeed, we were very excited when we learnt that MamL1 was found to be a high confidence CDK8 target and we looked hard in the Mam sequence for potential phosphorylation sites. Sadly, there is very little conservation between the fly and the mammalian proteins beyond the helical region that contacts CSL and NICD. Furthermore, there are no identifiable putative CDK8 phosphorylation sites based on conventional motifs. It therefore remains to be established whether or not Mam is a direct target of the CDK8 kinase activity. We have added an explanatory comment in the text (page 11).

Page 11: The authors write, "The differences in the effects on Mam and CSL imply that the CDK module is specifically involved in retaining Mam in the hub, and that in its absence other CSL complexes "win-out", either because the altered conditions favour them and/or because they are the more abundant." Are the "other" complexes the authors are referring to Hairless-containing complexes? With the reagents the authors have in hand couldn't this be explicitly shown for CSLcomplexes rather than speculated upon?

The reviewer is correct that CSL complexes containing Hairless are good candidates to be recruited in these conditions. We have compared the levels of Hairless at E(spl)-C following treatments with Senexin and have not detected a difference. However, it appears that the high proportion of unbound Hairless makes it difficult to detect/quantify the enrichment at E(spl)-C. We have therefore taken a different strategy, which is to measure the recruitment of a mutant form of CSL that is compromised for Hairless binding. Recruitment of the mutant CSL is detected in Notch-ON conditions, but is significantly reduced/absent following Senexin treatment. These data favour the model proposed by the reviewer that in the absence of CDK8 activity, the CSL-Hairless complexes win out. These new data have been added in new Supplementary Figure S3F and S3G (and see text page 11)

Page 12/13: The authors write, "Based on these results we propose that, after Notch activity decays, the locus remains accessible because when Mam-containing complexes are lost they are replaced by other CSL complexes (e.g. co-repressor complexes)." Again, why not actually test this hypothesis rather than speculate? The dynamics of Hairless complexes following the removal of Notch would be very interesting and build upon previously published results from the Bray lab.

We thank the reviewer for this comment and we agree it’s possible that the proportion of Hairless complexes increases after Notch withdrawal. However, for the reasons outlined above, it is difficult to quantify changes in Hairless, (and our preliminary experiment did not reveal any large-scale effect) and because of the complexity of the genetics we cannot straightforwardly extend the experiment to analyze the behaviour of the mutant CSL as above. Therefore, at present, we cannot say whether the loss of Mam is compensated by an increase in Hairless. We hope in future to investigate the characteristics of the memory in more depth.

Page 13: The authors write, "As Notch removal leads to a loss of Mam, but not CSL, from the hub, it should recapitulate the effects of MamDN." While the data in Figure 5B seem to support this hypothesis, it's not clear to me that the loss of Mam and MamDN should phenocopy each other, bc in the case of MamDN, NICD would still be present.

We apologise that this sentence was a bit misleading. We have now rewritten it to improve accuracy (page 13) “As Notch removal leads to a loss of Mam, but not CSL, from the hub, we hypothesised it would recapitulate the effects of MamDN on chromatin accessibility and transcription of targets.”

The temporal dynamics for Mam recruitment using the temperature- and optogenetic-paradigms are quite different. For example, in the optogenetic time course experiments, the preactivated cells are in the dark for 4 hours, while in the temperature-controlled experiments, there is still considerable enrichment of Mam at 4 hours. For the preactivated optogenetic experiments, how sure are the authors that Mam is completely gone from the locus, and alternatively, can the optogenetic experimental results be replicated in the temperature-controlled assays? My concern is whether the putative "memory" observation is just due to incomplete Mam removal from the previous activation event.

We appreciate the concerns of the reviewer. However, we are confident that the 4-hour optogenetic inactivation is much more effective than the equivalent time for temperature shifts. The temperature sensitive experiment involves a longer decay, because not only the protein but also the mRNA has to decay to fully remove NICD activity. The optogenetic experiments, involve only protein decay and so are more acute. Furthermore, we have tested (and we show in Figure 5H) that Mam is fully depleted after 4 hours “Off” in the optogenetic experiments.

In order to further strengthen the evidence in favour of the memory hub, we have extended the time-frame further to show that CSL is retained at the locus even after 24 hours “Notch OFF” in both the temperature and the optogenetic paradigm. We have also measured the effects on transcription after a 24hr OFF period using the optogenetic paradigm and seen that robust transcription is initiated in cells that have experienced a previous activation (preactivated) compared to those that have not (naïve). These new data have been added to new Figure 5 C-F and strongly support the memory model.

Reviewer #3 (Public Review):

Summary:

DeHaro-Arbona and colleagues investigate the in vivo dynamics of Notch-dependent transcriptional activation with a focus on the role of the Mastermind (MAM) transcriptional co-activator. They use GFP and HALO-tagged versions of the CSL DNA-binding protein and MAM to visualize the complex, and Int/ParB to visualize the site of Notch-dependent E(Spl)-C transcription. They make several conclusions. First, MAM accumulates at E(Spl)-C when Notch signaling is active, just like CSL. Second, MAM recruits the CDK module of Mediator but does not initiate chromatin accessibility. Third, after signaling is turned off, MAM leaves the site quickly but CSL and chromatin accessibility are retained. Fourth, RNA pol II recruitment, Mediator recruitment, and active transcription were similar and stochastic. Fifth, ecdysone enhances the probability of transcriptional initiation.

Strengths:

The conclusions are well supported by multiple lines of extensive data that are carefully executed and controlled. A major strength is the strategic combination of Drosophila genetics, imaging, and quantitative analyses to conduct compelling and easily interpretable experiments. A second major strength is the focus on MAM to gain insights into the dynamics of transcriptional activation specifically.

We thank the reviewer for their positive comments about the strengths of our work.

Weaknesses:

Weaknesses are minor. There were no p-values reported for data presented in Figure S1D and no indication of how variable measurements were. In addition, the discussion of stochasticity was not integrated optimally with relevant literature.

We thank the reviewer for noting these points. The statistical tests have now been included for Figure S1D (now Figure S1F). We have amplified the discussion about stochasticity, to include more reference to the literature and to make clear also the distinction with transcription bursting (page 19, 20).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The authors have an elegant series of manipulations that provide strong evidence for their hypotheses and conclusions. Their exploitation of a unique biological system amenable to imaging in the larval salivary gland is well-considered and well-performed. Most of the conclusions are supported by the data. I only have the concerns below.

(1) One of the main findings is the composition of Notch nuclear complexes and their interactions within a 'hub'. Yet most of the data showing hubs focus on labeling one protein component (+the locus or transcription), but multi-color imaging is rarely used to show how CSL-Mam, Mam-Med... protein signals coalescence to form a hub. Given the powerful tool developed, it would be important to show these multi-state hubs. Related to this, if the authors expect that hubs are formed independently of transcription or Notch pathway activation, do the authors see clustering at other non-specific loci in the nucleus? If not, can the authors comment on why they think that is the case? If so, do they demonstrate consistent residence time profiles with the tracked E(spl) locus?

We apologise that it was not evident from the data shown that the proteins co-localize. First we stress that all the experiments are multicolor and most rely on very powerful methods to measure co-recruitment at a chromosomal locus- something that is very rarely achieved by others studying hubs. Second, we have in all cases confirmed that the proteins do colocalize. We have modified the diagram of our analysis pipeline to make more clear that this relies on multi-colour imaging, and adjusted all the figure labels to indicate the position of E(spl)-C. We have also added panels to new supplementary Figure S1C with examples of the co-localization between CSL and Mam and a plot confirming their levels of recruitment are correlated across multiple nuclei.

We would like to clarify that our data show that the hubs do require Notch activation for their establishment. Other regions of enrichment are detected in Notch-ON conditions, but these are less prominent and, with no independent method for identifying them, can’t be compared between nuclei. In SPT experiments, other clusters with consistent residence are detected as reported in our recent paper which expanded on the SPT data (Baloul et al, 2023). We also detect co-localizations and “hubs” in other tissues, but those analyses are ongoing and beyond the scope of this paper.

(2) The authors convincingly show that Notch hub complexes exhibit a memory. While the data showing rapid hub reformation upon Notch withdrawal are solid and convincing (Figure 5, in particular, F), the claim that this memory fosters rapid transcriptional reactivation is less clear. Yet in order to invoke transcriptional memory, it's necessary to solidify this transcriptional response angle. The authors should consider quantifying the changes in transcription activity (at the TS and not in the cytoplasm as currently shown), as well as the timing of transcriptional reactivation (with the MS2 system or smFISH). Manipulating the duration of the activation and dark recovery periods could help to draw a better correlation between the timing of hub reformation and that of transcriptional response and would also help determine how persistent this phenomenon is.

We thank the reviewer for these suggestions. We have carried out several new experiments to probe further the persistence of memory and to show the effects on transcription when Notch is inactivated/reactivated. First, we have extended the time period for Notch inactivation by temperature control and show that the CSL hub persists even at 24 hours and that no transcription from the target E(spl)m3 is detected –neither at the transcription start-site nor in the cytoplasm. Second, we have extended the Notch OFF time period to 24 hours using the optogenetic approach and show that transcription is robustly reinitiated in preactivated nuclei when Notch is re-activated with 30 mins light treatment while little if any E(spl)m3 transcription is detected in naïve nuclei with the same treatment. These new data are included in new Figure 5 C-F and see page 13-14. Both these new experiments substantiate the model that the nuclei retain transcriptional memory.

(3) The manuscript ends with the finding that the presence of a Mam hub does not always correlate with transcription. They conclude that transcription is initially stochastic. The authors find this surprising and even state that this could not be observed without their in vivo live imaging approaches. I don't understand why this result is surprising or unexpected, as we now know that transcription is generally a stochastic process and that most (if not all) loci are transcribed in a bursting manner. The fact that E(spl)-C locus is bursty is already obvious from the smFISH data. The fact that active nascent transcription does not correlate with local TF hubs was already observed in early Drosophila embryos (with Zelda hubs and two MS2 reporters, hb-MS2, sna-MS2). If, in spite of the inherent stochasticity of transcription (bursting), the data are surprising for other reasons, the authors should explain it better.

We apologise that we had not made clear the reasons why the results were unexpected. We have substantially rewritten this section, and the discussion section, to clarify. We have also moderated the language used to better reflect the overall context of our results. We briefly summarise here. As the reviewer correctly states, it is well known that transcription is inherently bursty. Indeed the MS2 transcription profiles in “ON” nuclei are bursty, which likely reflects the switching of the promoter. However, in other contexts where we have monitored transcription although it is bursty it has nevertheless been initiated synchronously in response to Notch in all nuclei in a manner that was fully penetrant. What we observe in our current conditions, is that some nuclei never initiate transcription over the time-course of our experiments (2-3 hours), and those that are ON rarely switch off. This implies that there is another rate-limiting step. Supplying a second signal can modulate this so that it occurs with much higher frequency/penetrance. We consider this to be a second tier of regulation above the fundamental transcriptional bursting.

The fact that Mam is recruited in all nuclei, whether or not they are actively transcribing was surprising because recruitment of the activation complex has been considered as the limiting step. This is somewhat different from Zelda, which is thought to be permissive and needed at an early step to prime genes for later activation rather than to be the last step needed to fire transcription. We note also that we are not monitoring the position of the hub with respect to the promoter, as in the Zelda experiments (Zelda hubs may still persist, but they are not overlapping with the nascent RNA), we are monitoring the presence or absence of Mam hub in proximity to a genomic region.

Minor suggestions:

(1) The genotypes of the samples should be indicated in the figure legends.

We thank the reviewer for this suggestion. We have provided a table (new Table S3) where all of the genetic combinations are provided in detail for each figure. We considered that this approach would be preferable because it would be quite cumbersome to have the genotypes in each legend as they would become very long and repetitive.

(2) While the schematic Fig1A explains how the locus is detected, the presence of ParS/ParB is never indicated in subsequent panels and Figure. I assume that all panels depicting enrichment profiles, use a given radius from the ParS/ParB dot to determine the zero of the x-axis (grey zone). This should be clearly stated in all panels/figure legends concerned.

We apologies if this was not made explicit. Yes, all panels depicting enrichment profiles, use immunofluorescence signal from ParA/ParB recruitment to determine the zero of the x-axis. We have now marked this more clearly In all figures (grey bar, grey shading or labelled 0). All images where the locus is indicated by an arrowhead, by a coloured bar above the intensity plots or by grey shading in the graphs have been captured with dual colour and the signal from ParA/B recruitment used to define its location. This is now clearly stated in the analysis methods and in the legend. We have also modified the diagram in new supplementary Figure S1B, showing our analysis pipeline, to make that more explicit.

(3) FRAP/SPT experiments: the author should provide more details. How many traces? Are traces showing bleaching removed?

P7: does the statement ' The residences are likely an underestimation because bleaching and other technical limitations also affect track durations' imply that traces showing bleaching have not been removed from the analysis?

The authors could justify the choice of the model for fitting FRAP/Spt experiments and be cautious about their interpretation. For example, interpreting a kinetic behavior as a DNA-specific binding event can be accurate, only if backed up with measurements with a mutant version of the DNA binding domain.

We apologise if some of this information was not evident. The number of trajectories is provided in new Figure S1F, which indicates the number of trajectories analyzed for each condition in Figure 1.

We have now added also the numbers of trajectories analyzed for the ring experiments.

The comments on page 7 about bleaching refer to the technical limitations of the SPT approach. However, as bleached particles cannot be distinguished from those that leave the plane of imaging, they have not been filtered or removed. We have not sought to make claims about absolute residence times for that reason. Rather the point is to make a comparison between the different molecules. As the same fluorescent ligand and imaging conditions are used in all the experiments, all the samples are equivalently affected by bleaching. We subdivide trajectories according to their properties and infer that those which are essentially stationary are bound to chromatin, as is common practice in the field. We note that we have previously shown that a DNA binding mutant of CSL does not produce a hub at E(spl)-C in Notch-ON conditions and has a markedly more rapid recovery in FRAP experiments (Gomez-Lamarca et al, 2018) consistent with the slow recovery being related to DNA binding. This point has been added to the text (page 8).

(4) The authors should quantify their RNAi efficiency for Hairless-RNAi, Med13-RNAi, white-RNAi, yellow-RNAi, CBP-RNAi, and CDK8-RNAi.

We thank the reviewer for this comment. We have made sure that we are using well validated RNAis in all our experiments and have included the references in Table S2 where they have been used. We have now evaluated the knock-down in the precise conditions used in our experiments by quantitative RT-PCR and added those data, which show efficient knock-down is occurring, to new Supplementary Figure S1D and Figure S3J. We note also that the RNAi experiments are complemented by experiments inhibiting the complexes with specific drugs and that these yield similar results.

(5) Figure 3 A: could the author show that transcription is indeed inhibited upon triptolide treatment with smFISH (with for example m3 probes)? Why not use alpha-amanitin?

We thank the reviewer for this suggestion. We had omitted the smFISH data from this experiment in error. These data have now been added to new Supplementary Figure S3A and clearly show that transcription is inhibited following 1 hour exposure to triptolide. Triptolide is a very fast acting and very efficient inhibitor of transcription that acts at a very early step in transcription initiation. In our experience it is much more efficient than alpha-amanitin and is now the inhibitor of choice in many transcription studies.

(6) Figure 4 typo: panel B should be D and vice versa. Accessibility panels are referred to as Figure 4D, D' in the text but presented as panel B in the Figure.

We thank the reviewer for noting this mistake, it is now changed in the main text.

(7) The authors must add their optogenetic manipulation protocol to their methods section.

The method is described in detail in a recently published paper that reports its design and use. We have now also added a section explaining the paradigm in the methods (Page 31) as requested.

(8) Figure 3G needs a Y-axis label.

Our apologies, this has now been added.

(9) The authors should note why there was a change of control in Figure 3D compared to 3E and G (yellow RNAi vs white RNAi).

This is a pragmatic choice that relates to the chromosomal site of the RNAis being tested. Controls were chosen according to the chromosome that carries the UAS-RNAi: for the second chromosome this was yellow RNAi and for the third white RNAi. This is explained in the methods.

(10) Figure 1 would benefit from a diagram describing the genomic structure of the E(spl) locus and the relative position of the labelled locus within it.

We thank the reviewer for this suggestion and have added a diagram to Supplementary Figure S1A .

Reviewer #2 (Recommendations For The Authors):

Minor criticisms and typos:

Pet peeve: in some of the figure panels they are labeled Notch ON or OFF, but in others they are not, albeit that info is included in the figure legend. For the ease of the reader/reviewer, would it be possible to label all relevant figure panels either Notch ON or OFF for clarity?

We thank the reviewer for this suggestion and have modified the figures accordingly.

Page 7, top. "In comparison to their average distribution across the nucleus, both CSL and Mam trajectories were significantly enriched in a region of approximately 0.5 μm around the target locus in Notch-ON conditions, reflecting robust Notch dependant recruitment to this gene complex." Are the authors referring to Figure 1D here?

Thank you, this figure call-out has been added in the text.

Page 9. "...reported to interact with p300 and other factors (Figure S2B)." I believe the authors mean Figure S2C and not S2B.

Thank you, this has been corrected in the text.

Page 9. There is no Figure S2D.

Apologies, this was referring to Figure S1D, and is now corrected in the text.

Page 11: "...were at very reduced levels in nuclei co-expressing MamDN (Figure 4B).." Should be Figure 4CD.

Thank you, this has been corrected in the text.

Page 12: "...which was maintained in the presence of MamDN (Figure 4D, D')." Should be Figure 4B.

Thank you, this has been corrected in the text.

Reviewer #3 (Recommendations For The Authors):

In the Results section on Hub, the paragraph starting with "Third, we reasoned . ." the callout to Figure S2D should be Fig S1D.

Thank you, this has been corrected in the text

Figures: The font size in the Figures is so small that most words and numbers cannot be read on a printout. One has to go to the electronic version and increase the size to read it. This reviewer found that inconvenient and often annoying.

We apologise for this oversight, the font size has now been adjusted on all the graphs etc.

Figure legends: the legends are terse and in some cases leave explanations to the imagination (e.g. "px" in Figure 2E). It would be useful to go through them and make sure those who are not a Drosophila Notch person and not a transcription biochemist can make sense of them.

Our apologies for the lack of clarity in the legends. We have gone over them to make them more accessible and less succinct.

eLife assessment

This fundamental study advances our understanding of how Notch signaling activates transcription by analyzing dynamics of the Mastermind transcriptional co-activator and its role in the activation complex. The evidence is compelling and based on state of the art methods with precise quantitative measurements.

Reviewer #2 (Public Review):

The manuscript from deHaro-Arbona et al, entitled "Dynamic modes of Notch transcription hubs conferring memory and stochastic activation revealed by live imaging the co-activator Mastermind", uses single molecule microscopy imaging in live tissues to understand the dynamics and molecular determinants of transcription factor recruitment to the E(spl)-C locus in Drosophila salivary gland cells under Notch-ON and -OFF conditions. Previous studies have identified the major players that are involved in transcription regulation in the Notch pathway, as well as the importance of general transcriptional coregulators, such as CBP/P300 and the Mediator CDK module, but the detailed steps and dynamics involved in these processes are poorly defined. The authors present a wealth of single molecule data that provides significant insights into Notch pathway activation, including:

(1) Activation complexes, containing CSL and Mam, have slower dynamics than the repressor complexes, containing CSL and Hairless.<br /> (2) Contribution of CSL, NICD, and Mam IDRs to recruitment.<br /> (3) CSL-Mam slow-diffusing complexes are recruited and form a hub of high protein concentrations around the target locus in Notch-ON conditions.<br /> (4) Mam recruitment is not dependent on transcription initiation or RNA production.<br /> (5) CBP/P300 or its associated HAT activity is not required for Mam recruitment<br /> (6) Mediator CDK module and CDK8 activity is required for Mam recruitment, and vice-versa, but not CSL recruitment.<br /> (7) Mam is not required for chromatin accessibility but is dependent on CSL and NICD.<br /> (8) CSL recruitment and increased chromatin accessibility persist after NICD removal and loss of Mam, which confers a memory state that enables rapid re-activation in response to subsequent Notch activation<br /> (9) Differences in the proportions of nuclei with both Pol II and with Mam enrichment, which results in transcription being probabilistic/stochastic. These data demonstrate that presence of Mam-complexes is not sufficient to drive all the steps required for transcription in every Notch-ON nucleus.<br /> (10) The switch from more stochastic to robust transcription initiation was elicited when ecdysone was added.

Overall, the manuscript is well written, concise, and clear, and makes significant contributions to the Notch field, which are also important for a general understanding of transcription factor regulation and behavior in the nucleus. The authors have satisfactorily addressed all my criticisms of their initial submission and therefore congratulate the authors on an excellent paper.

Reviewer #3 (Public Review):

Summary:

DeHaro-Arbona and colleagues investigate the in vivo dynamics of Notch-dependent transcriptional activation with a focus on the role of the Mastermind (MAM) transcriptional co-activator. They use GFP and HALO-tagged versions of the CSL DNA-binding protein and MAM to visualize the complex, and Int/ParB to visualize the site of Notch-dependent E(Spl)-C transcription. They make several conclusions. First, MAM accumulates at E(Spl)-C when Notch signaling is active, just like CSL. Second, MAM recruits the CDK module of Mediator but does not initiate chromatin accessibility. Third, after signaling is turned off, MAM leaves the site quickly but CSL and chromatin accessibility are retained. Fourth, RNA pol II recruitment, Mediator recruitment and active transcription were similar and stochastic. Fifth, ecdysone enhance the probability of transcriptional initiation.

Strengths:

The conclusions are well supported by multiple lines of extensive data that is carefully executed and controlled. A major strength is the strategic combination of Drosophila genetics, imaging and quantitative analyses to conduct compelling and easily interpretable experiments. A second major strength is the focus on MAM to gain insights into dynamics of transcriptional activation specifically.

Weaknesses:

Weaknesses were minor. and have been addressed in the revised manuscript.

Author Response

We are very pleased to hear the overall positive views and constructive criticisms of eLife Editors and Reviewers on our work. In particular, we appreciate their comments highlighting the value of our new pipeline for high-throughput quantification of fly embryonic movement and the positive views of reviewers and editors that our data on the roles of miR-2b-1 in embryonic movement are well supported.

Regarding Reviewer 1, we thank them for their positive comments that our work is experimentally sound and well-written, their kind words on the value of our new embryonic movement pipeline, and their overall appreciation of the quality, scope, and significance of our work. In a revised version of the manuscript we will consider discussing and addressing some of the interesting points raised by Rev1.

Turning to the comments by Rev2, we are grateful to them for their recognition of the novelty of our miRNA findings and appreciation of the utility of our novel quantitative pipeline for assessing embryonic movement. Nonetheless, we politely – but strongly – disagree with their suggestion that the findings are inflated by our language. For example, they criticise our use of the verb ‘control’, yet this is a standard textbook term in molecular biology to describe biological processes regulated by genetic factors: given that miR-2b-1 regulates movement patterns during embryogenesis, to say that miR-2b-1 ‘controls’ embryonic movement in the Drosophila embryo is reasonable and in line with the language used in the field. It is not inflation. In connection to other comments, in a revised manuscript we will propose a different name for the gene here described as Janus to avoid annotation issues at FlyBase due to other, unrelated genes that include this word as part of their names.

eLife assessment

This important study presents a new quantitative imaging pipeline that describes with high temporal precision and throughput the movements of late-stage Drosophila embryos, a critical moment when motion first appears. A new approach is used to explore the role of miRNAs in motion onset and presents solid evidence that shows a role for miR-2b-1 and its target Janus in embryonic motion. The data are well supported but do not provide mechanistic insight into the emergence of movement while the writing inflates the importance of the conclusions. The authors must change the name of Janus which is already used in Drosophila genetics.

Reviewer #1 (Public Review):

Summary:

This is an experimentally soundly designed work and a very well-written manuscript. There is a very clear logic that drives the reader from one experiment to the next, the experimental design is clearly explained throughout and the relevance of the acquired data is well analyzed and supports the claims made by the authors. The authors made an evident effort to combine imaging, genetic, and molecular data to describe previously unknown early embryonic movement patterns and to identify regulatory mechanisms that control several aspects of it.

Strengths:

The authors develop a new method to analyze, quantitatively, the onset of movement during the latter embryonic stages of Drosophila development. This setup allows for a high throughput analysis of general movement dynamics based on the capture of variations of light intensity reflected by the embryo. This setup is capable of imaging several embryos simultaneously and provides a detailed measure of movement over time, which proves to be very useful for further discoveries in the manuscript. This setup already provides a thorough and quantifiable description of a process that is little known and identifies two different phases during late embryonic movements: a myogenic phase and a neurogenic phase, which they elegantly prove is dependent on neuronal activity by knocking down action potentials across the nervous system.

However, in this system, movement is detected as a whole, and no further description of the type of movement is provided beyond frequency and amplitude; it would be interesting to know from the authors if a more precise description of the movements that take place at this stage can be achieved with this method (e.g. motion patterns across the A-P body axis).

Importantly, this highly quantitative experimental setup is an excellent system for performing screenings of motion regulators during late embryonic development, and its use could be extended to search for different modulators of the process, beyond miRNAs (genetic mutants, drugs, etc.).

Using their newly established motion detection pipeline, the authors identify miR-2b-1 as required for proper larval and embryonic motion, and identify an overall reduction in the quantity of both myogenic and neurogenic movements, as well as an increased frequency in neurogenic movement "pulses".

Focusing on the neurogenic movement phenotype the authors use in situ probes and perform RT-PCR on FACS-sorted CNS cells to unambiguously detect miR-2b-1 expression in the embryonic nervous system. The neurogenic motion defects observed in miR-2b-1 mutant embryos and early larvae can be completely rescued by the expression of ectopic miR-2b-1 specifically in the nervous system, providing solid evidence of the requirement and sufficiency of miR-2b-1 expressed in the nervous system to regulate these phases of movement.

To explore the mechanism through which miR-2b-1 impacts embryonic movement, the authors use a state-of-the-art bioinformatic approach to identify potential targets of miR-2b-1, and find that the expression levels of an uncharacterized gene, CG3638, are indeed regulated by miR-2b-1. Furthermore, they prove that by knocking down the expression of CG3638 in a miR-2b-1 mutant background, the neurogenic embryonic movement defects are rescued, pointing that the repression of CG3638 by miR-2b-1 is necessary for correct motion patterns in wild-type embryos. Therefore, this paper provides the first functional characterization of CG3638, and names this gene Janus.

Finally, the authors aim to discriminate which elements of the embryonic motor system miR-2b-1/Janus are required. Using directed overexpression of miR-2b-1 and Janus knockdown in the motor neurons and the chordotonal (sensory) organs, they prove that the miR-2b-1/Janus regulatory axis is specifically required in the sensory organs to promote normal embryonic and larval movement.

Weaknesses:

The authors do not describe properly how the miRNA screening was performed and just claim that only miR-2b-1 mutants presented a defective motion phenotype in early L1. How many miRNAs were tested, and how candidates were selected is never explicitly mentioned in the text or the Methods section.

The initial screening to identify miRNAs involved in motion behaviors is performed in early larval movement. The logic presented by the authors is clear - it is assumed that early larval movement cannot proceed normally in the absence of previous embryonic motion - and ultimately helped them identify a miRNA required for modulation of embryonic movement. However, it is possible that certain miRNAs play a role in the modulation of embryonic movement while being dispensable for early L1 behaviors. Such regulators might have been missed with the current screening setup.

Although similar changes to those described for the neurogenic phase of embryonic movement are described for the myogenic phase in miR-2b-1 mutants (reduction in motion amplitude), this phenotype goes unexplored. This is not a big issue, as the authors convincingly demonstrate later that miR-2b-1 is specifically required in the nervous system for proper embryonic and larval movement, and the effects of miR-2b-1 on myogenic movement might as well be the focus of future work. However, it will be interesting to discuss here the implications of a reduced myogenic movement phase, especially as miR-2b-1 is specifically involved in regulating the activity of the chordotonal system - which precisely detects early myogenic movements.

FACS-sorting of neuronal cells followed by RT-PCR convincingly detects the presence of miR-2b-1 in the embryonic CNS. However, control of non-neuronal cells would be required to explore whether miR-2b-1 is not only present but enriched in the nervous system compared to other tissues. This is also the case in the miR-2b-1 and Janus expression analysis in the chordotonal organs: a control sample from the motor neurons would help discriminate whether miR-2b-1/Janus regulatory axis is specifically enriched in chordotonal organs or whether both genes are expressed throughout the CNS but operate under a different regulation or requirements for the movement phenotypes.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript, "A microRNA that controls the emergence of embryonic movement" by Menzies, Chagas, and Alonso provides evidence that Drosophila miR-2b-1 is expressed in neurons and controls the expression of the predicted chloride channel CG3638, here named "Janus". Loss of the miRNA leads to movement phenotypes that can be rescued by downregulation of Janus; using specific drivers, the authors show that a larval movement phenotype (slower movement) can be rescued by knockdown of Janus in the chordotonal organs, suggesting that the increase in Janus found in the chordotonal organs is likely the root of the movement defects. Overall, I found the data presented in the manuscript of reasonable quality and are well enough supported by the presented data. That being said, I do have a few problems with the manuscript, mostly stemming from what I feel is an inflated presentation of the importance of the findings.

Strengths:<br /> The genetic and phenotypic analysis seems to be correct. The nicest part of the manuscript is the connection between the loss of a miRNA and finding its likely target in generating a phenotype. The authors also develop some protocols for the analysis of the movement phenotypes which may be useful for others.

Weaknesses:<br /> As I mentioned above, I felt the presentation was a bit overstated. The authors present their data in a way that focuses on movement, the emergence of movement, and how their miRNA of interest is at the center of this topic. I only point to the title and name that they wish to give the target of their miRNA to emphasize this point. "Janus" the god of movement and change. The results and discussion section starts with a paragraph saying, "Movement is the main output of the nervous system... how developing embryos manage to organise the necessary molecular, cellular, and physiological processes to initiate patterned movement is still unknown. Although it is clear that the genetic system plays a role, how genes control the formation, maturation and function of the cellular networks underlying the emergence of motor control remains poorly understood." While there is nothing inherently untrue about these statements, it is a question of levels of understanding. One can always argue that something in biology is still unknown at a certain level. However, one could also argue that much is known about the molecular nature of movement. Next, I am not sure how much this work impacts the area of study regarding the emergence of movement. The authors show that a reduction of a miRNA can affect something about certain neurons, that affects movement. The early movements, although slightly diminished, still emerge. Thus, their work only suggests that the function of some neurons, or perhaps the development of these neurons may impact the early movements. This is not new as it was known already from early work from the Bate lab.

Later larval movements were also shown to be modified in the miRNA mutants and were traced to "janus" overexpression in the chordotonal organs. As neurons are quite sensitive to the levels of Cl- and Janus is thought to be a Cl- channel, this could lead to a slight dysfunction of the chordotonal neurons. So, based on this, the work suggests that dysfunction of the chordotonal organs could impact larval movement. This was, of course, already known. The novelty of this work is in the genes being studied (important or not). We now know that miR 2b-1 and Janus are expressed in the early neurons and larval chordotonal neurons and their removal is consistent with a role for these genes in the functioning of these neurons. This is not to trivialize these findings, simply to state that these results are not significantly changing our overall understanding of movement and the emergence of movement. I would call it a stretch to say that this miRNA 'controls' the emergence of movement, as in the title.

Finally, the name Janus should be changed as it is already being used. A quick scan of flybase shows that there is a Janus A and B in flies (phosphatases) and I am surprised the authors did not check this. I was initially worried about the Janus kinase (JAK) when I performed the search. While I understand that none are only called Janus, studies of the jan A and B genes refer to the locus as the janus region, which could lead to confusion. The completely different molecular functions of the genes relative to CG3638 add to the confusion. Thus, I ask that the authors change the name of CG3638 to something else.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

This work provides new mechanistic insights into the competitive inhibition in the mammalian P2X7 receptors using structural and functional approaches. The authors solved the structure of panda (pd) P2X7 in the presence of the classical competitive antagonists PPNDS and PPADS. They find that both drugs bind to the orthosteric site employed by the physiological agonist ATP. However, owing to the presence of a single phosphate group, they prevent movements in the flipper domain required for channel opening. The authors performed structure-based mutational analysis together with electrophysiological characterization to understand the subtype-specific binding of these drugs. It is known from previous studies that P2X1 and P2X3 are more sensitive to these drugs as compared to P2X7, hence, the residues adjacent to the ATP binding site in pdP2X7 were mutated to those present in P2X1. They observed that mutations of Q143, I214, and Q248 into lysine (hP2X1) increased the P2X7 sensitivity to PPNDS, whereas in P2X1, mutations of these lysines to alanine reduced sensitivity to PPNDS, suggesting that these key residues contribute to the subunit-specific sensitivity to these drugs. Similar experiments were done in hP2X3 to demonstrate its higher sensitivity to PPNDS. This preprint provides a useful framework for developing subtype-specific drugs for the family of P2X receptor channels, an area that is currently relatively unexplored.

We appreciate the time and effort Reviewer #1 devoted to this review, and we have addressed the specific comments below.

(1) Why was the crystallization construct of panda P2X7 used for structural studies instead of rat P2X7 with the cytoplasmic ballast which is a more complete receptor that is closely related to the human receptor? Can the authors provide a justification for this choice?

We appreciate this comment. We did try to express the rat P2X7 receptor in its full-length form based on a previous report (Cell 2019, PMID: 31587896), but the expression of the receptor was not successful for an unknown reason. Instead, we employed a truncated construct of panda P2X7 based on the findings described another previous report (eLife 2016, PMID: 27935479). This truncated construct also possesses ATP-dependent channel activity (eLife 2016, PMID: 27935479). Thus, we understand that the full-length P2X7 construct would be preferable, particularly for addressing the function of the cytoplasmic domain; however, the main focus of this study was on PPNDS/PPNADS recognition and the associated structural changes in the ATP binding pocket, which we believe are less likely to be severely affected by truncation of the cytoplasmic domain. In support of this expectation, our mutational analyses are consistent with the structures in this study. Therefore, we believe that the use of the truncation construct in this study is justified.

(2) Was there a good reason why hP2X1 and hP2X3 currents were recorded in perforated patches, whereas pdP2X7 currents were recorded using the whole-cell configuration? It seems that the extent of rundown is less of a problem with perforated patch recordings. Can the authors comment and perhaps provide a justification? It would also be good to present data for repeated applications of ATP alone using protocols similar to those for testing antagonists so the reader can better appreciate the extent of run down with different recording configurations for the different receptors.

We thank the reviewer for bringing up this point. The whole-cell configuration is the most commonly used method in patch-clamp experiments; therefore, we used this method to record the current of pdP2X7 (Author response image 1). However, the whole-cell configuration is not suitable for all experiments; for example, the currents of P2X1 and P2X3 recorded by this method show a severe "rundown" effect. The "rundown" effect prevents accurate calculation of the inhibition rate of the antagonist, and to obtain more accurate results, we used perforated patches to record the currents of hP2X1 and hP2X3.

Author response image 1.

Representative current traces of pdP2X7, hP2X3, and hP2X1 after repeated applications of ATP. The pdP2X7 currents were recorded using the whole-cell configuration, and the hP2X1 and hP2X3 currents were recorded using perforated patches.

(3) The data in Fig. S1, panel A shows multiple examples where the currents activated by ATP after removal of the antagonist are considerably smaller than the initial ATP application. Is this due to rundown or incomplete antagonist unbinding? It is interesting that this wasn't observed with hP2X1 and hP2X3 even though they have a higher affinity for the antagonist. Showing examples of rundown without antagonist application would help to distinguish these distinct phenomena and it would be good for the authors to comment on this in the text. It is also curious why a previous study on pdP2X7 did not seem to have problems with rundown (see Karasawa and Kawate. eLife, 2016).

We thank the reviewer for bringing up this point. We believe that this difference may be the result of incomplete antagonist unbinding. A similar phenomenon has been observed in previous studies of pdP2X7 (eLife 2016, PMID: 27935479). In the previous experiment, the currents activated by ATP after removal of the antagonist A740003 did not return to the initial value upon ATP application, whereas activation by ATP after removal of the antagonist GW791343 immediately restored the initial value upon ATP application (Fig. 1C of eLife 2016, PMID: 27935479). This may be because different inhibitors dissociate differently from pdP2X7. In our experiments, we assumed that PPNDS/PPADS was not completely dissociated from P2X7 even after 20 min of elution. The activation of P2X7 by ATP without antagonists showed no rundown effect (Author response image 1); therefore, we calculated the inhibition rate of the antagonist according to the precontrol.

(4) The written presentation could be improved as there are many instances where the writing lacks clarity and the reader has to guess what the authors wish to communicate.

To address this comment, we made changes to the text, particularly by following the

Recommendations for The Authors

Reviewer #1 (Recommendations For The Authors):

(1) The way the manuscript is written could be greatly improved. There are many confusing sections where the reader has to guess what the authors wish to convey. For example, on page 9 "In addition, the mutation of Val173 to aspartate, as observed in pdP2X7, significantly decreased the sensitivity to PPNDS (Fig. 6B)." It appears from this sentence that Asp is present in P2X7, which is incorrect, please rephrase. There are many more examples of confusing sentences that need to be carefully edited to improve comprehension.

To address this comment, we extensively modified the text to avoid this kind of misunderstanding. Please see the manuscript file with the track changes.

(2) Please use either a 1-letter or 3-letter code for amino acid residues throughout the manuscript to maintain uniformity.

We made this correction throughout the revised manuscript.

(3) In Figure 1 on the right side, including the nearby density and side chains for interacting residues of PPNDS and PPADS would give more information and reliability for the density of the drugs.

We appreciate this comment. The corresponding information is shown in Fig. S7.

(4) Typo: Figure S1, E, and F panels - please correct the y-axis label to Inhibition.

We corrected the typo in Fig. S1.

(5) Please rewrite the legends for Fig. S3 and S5. They are confusing. The figure shows 3D classification using Relion, however, the legend suggests it was done using Cryosparc. Please clarify.

We apologize for the confusion. Before applying C3 symmetry, all steps including 3D classification were performed in Relion 3.1. With C3 symmetry, we performed further refinement using Cryosparc v4.2.1 by non-uniform refinement. We have corrected the figure legends accordingly.

(6) For Fig. S3 and S5 increase the resolution and size of representative micrographs, and also please provide scale bars.

We have corrected Figures S3 and S5 accordingly.

(7) Please add the 3D classification protocol performed in Relion/Cryosparc in the methods section as well.

We added the corresponding description to the revised manuscript (Lines 9-14, Page 16).

(8) In Table S1, under the initial model the authors state 'this study' when they should report the use of 5U1L according to the methods section.

We corrected Table S1 in accordance with this comment.

(9) The authors should consider combining the raw data shown in Figure S1 in Figure 6 as it provides stronger support for the conclusions than the bar graphs shown in Figure 6B.

We appreciate the comment and fully understand the intention of Reviewer #1. Nevertheless, we would like to keep Figure S1, since it was also mentioned earlier together with Figure 1. In addition, if we combine Figure S1 with Figure 6, the result would be too large to present as a single figure.

(10) In Figure 6A, please provide colored labels for both P2X7 and P2X1 to aid comprehension of the structural models.

Based on this comment, we corrected the labels in Figure 6.

(11) In the discussion, the authors write about comparisons with the docking study by Huo et al. JBC, 2018. Can they show the superimposition of their EM model with the previous studies' docking model in a supplementary figure for more clarity?

We appreciate the constructive comments. However, unfortunately, the docking model in the previous study (JBC 2018, PMID: 29997254) is not available, so it is not possible to show the superimposition.

Reviewer #2 (Public Review):

Summary:

P2X receptors play pivotal roles in physiological processes such as neurotransmission and inflammation, making them promising drug targets. This study, through cryo-EM and functional experiments, reveals the structural basis of the competitive inhibition of the PPNDS and PPADS on mammalian P2X7 receptors. Key findings include the identification of the orthosteric site for these antagonists, the revelation of how PPADS/PPNDS binding impedes channel-activating conformational changes, and the pinpointing of specific residues in P2X1 and P2X3 subtypes that determine their heightened sensitivity to these antagonists. These insights present a comprehensive understanding that could guide the development of improved drugs targeting P2X receptors. This work will be a valuable addition to the field.

Strengths and weaknesses:

The combination of structural experiments and mutagenesis analyses offers a deeper understanding of the mechanism. While the inclusion of MD simulation is appreciated, providing more insights from the simulation might further strengthen this already compelling story.”

We appreciate the time and effort Reviewer #2 devoted to this review, and we have addressed the specific comments below.

Reviewer #2 (Recommendations For The Authors):

(1) On page 3, the sentence "ATP analogs are the most competitive inhibitors of P2X receptors but are typically unsuitable due to a lack of high specificity in vivo," might need additional context. Could the authors clarify if they are referring to the unsuitability of ATP analogs for medical applications?

To address this comment, we have rewritten the sentence as follows (Lines 13-16, Page 3):

ATP analogs are most common among competitive inhibitors for P2X receptors; however, they are generally unsuitable for in vivo applications due to their relatively low specificity, which may result in off-target toxicity. This issue arises because the human body contains numerous ATP-binding proteins.

(2) Fig. S1. I am curious why, for P2X7, the ATP-only current after removal of PPNDS/PPADS does not recover and become larger than the current in the presence of PPNDS/PPADS? Such behavior was not as pronounced in P2X1. Does that suggest PPNDS/PPADS might remain bound and can not be removed when the P2X7 channel is closed?

We thank the reviewer for bringing up this point. We believe that this difference may be the result of incomplete antagonist unbinding. A similar phenomenon has been observed in previous studies of pdP2X7 (eLife 2016, PMID: 27935479). In the previous experiment, the currents activated by ATP after removal of the antagonist A740003 did not return to the initial value upon ATP application, whereas activation by ATP after removal of the antagonist GW791343 immediately restored the initial value upon ATP application (Fig. 1C of eLife 2016, PMID: 27935479). We strongly agree with the reviewer that this may be due to the difficulty of dissociating the antagonist from pdP2X7.

eLife assessment

This study by Sheng and colleagues provides valuable insights into the mechanism of competitive inhibitors of P2X receptors. The structural and functional evidence supporting the subtype specificity of pyridoxal-5'-phosphate derivatives is compelling and provides information for designing drugs that selectively target different subtypes of P2X receptor channels. The work will be of interest to biochemists, structural biologists, and pharmacologists.

Reviewer #1 (Public Review):

This work provides new mechanistic insights into the competitive inhibition in the mammalian P2X7 receptors using structural and functional approaches. The authors solved the structure of panda (pd) P2X7 in the presence of the classical competitive antagonists PPNDS and PPADS. They find that both the drugs bind to the orthosteric site employed by the physiological agonist ATP. However, owing to the presence of a single phosphate group, they prevent movements in the flipper domain required for channel opening. The authors performed structure based mutational analysis together with electrophysiological characterization to understand the subtype specific binding of these drugs. It is known from previous studies that P2X1 and P2X3 are more sensitive to these drugs as compared to P2X7, hence, the residues adjacent to the ATP binding site in pdP2X7 were mutated to those present in P2X1. They observed that mutations of Q143, I214 and Q248 into lysine (hP2X1) increased the P2X7 sensitivity to PPNDS, whereas in P2X1, mutations of these lysines to alanine reduced sensitivity to PPNDS, suggesting that these key residues contribute to the subunit specific sensitivity to these drugs. Similar experiments were done in hP2X3 to demonstrate its higher sensitivity to PPNDS. This preprint provides a useful framework for developing subtype specific drugs for the family of P2X receptor channels, an area that is currently relatively unexplored.<br /> The conclusions of the paper are well supported.

The revised manuscript is well written and presents its data with more clarity.

Reviewer #2 (Public Review):

Summary:

P2X receptors play pivotal roles in physiological processes such as neurotransmission and inflammation, making them promising drug targets. This study, through cryo-EM and functional experiments, reveals the structural basis of the competitive inhibition of the PPNDS and PPADS on mammalian P2X7 receptors. Key findings include the identification of the orthosteric site for these antagonists, the revelation of how PPADS/PPNDS binding impedes channel-activating conformational changes, and the pinpointing of specific residues in P2X1 and P2X3 subtypes that determine their heightened sensitivity to these antagonists. These insights present a comprehensive understanding that could guide the development of improved drugs targeting P2X receptors. This work will be a valuable addition to the field.

Strengths:

The combination of structural experiments and mutagenesis analyses offers a deeper understanding of the mechanism. While the inclusion of MD simulation is appreciated, providing more insights from the simulation might further strengthen this already compelling story.

Author Response:

Reviewer #1 (Public Review):

[...] Weaknesses are the absence of correlation between the results from the animal studies and human pancreatic cancers.

Author response: We appreciate the reviewer’s attention to the importance of human pancreatic cancer studies. In a previous study (D’Amico et al. Genes & Development 2018 doi: 10.1101/gad.311852.118), we evaluated the expression of STAT3 in human pancreatic tissue microarrays and data from the Human Protein Atlas. Mutations in Stat3 are infrequent in human pancreatic cancers, however there is a trend of decreased STAT3 activity in poorly differentiated carcinomas.

In the current study, STAT3 and SMAD4 gene signature scores (computed from KO KPC cells) were aligned with human pancreatic ductal adenocarcinoma samples from the TCGA cohort, and statistical analyses supported the selective antagonism of STAT3 and SMAD4 (Fig 4D, Fig 4E).

The complex process of EMT is difficult to characterize rigorously in human cancers. Mouse models offer an opportunity to study the relationships between cancer phenotypes and genetic alterations.

Reviewer #2 (Public Review):

[...] While correlations are strong, the study would benefit from additional cause-and-effect type experiments. It would also be beneficial to better tie together the first and second parts of the paper.

Author response: We understand the Reviewer’s interest in additional experiments that could further elucidate mechanisms that drive EMT and/or KRAS dependency in relation to STAT3 and TGF-beta antagonism. We previously investigated the development of mutant KRAS knockout tumors (Ischenko et al. Nature Communications 2021 doi:10.1038/s41467-021-21736) to find loss of KRAS promotes EMT, similar to loss of STAT3. Additional experiments are underway but are outside the scope of the current study.

The first part of the paper is mechanistic and used KRAS-transformed mouse embryo fibroblasts to perform in vitro studies with foci formation. The cell-based foci formation assay has been shown to best evaluate malignant transformation and oncogenic potential. In the second part we transitioned to epithelial cells and pancreatic ductal adenocarcinomas to combine mechanistic relationships with genetic models.

eLife assessment

This study aims to explore the diabetes-bone paradox using the Mendelian Randomization approach. That diabetes itself is not the direct cause, but rather the complications or associated risk factors increase the risk of fracture, constitutes a valuable insight. Mendelian randomization to explain the relationship of two complex conditions is solid and conducted properly; however, the efforts to reconcile the discrepancies between the Mendelian Randomization analysis and observational studies are incomplete.

Reviewer #3 (Public Review):

Summary:

The authors found two endosomal fusion modes by live cell imaging of endosomes in yolk sac lateral endoderm cells of 8.5-day-old embryonic mice and described the fusion modes by mathematical models and simulations. They also showed that actin polymerization is involved in the regulation of one of the fusion modes.

Strengths:

The strength of this study is that the authors' claims are well supported by beautiful live cell images and theoretical models. By using specialized cells, yolk sac visceral endoderm cells, the live images of endosomal fusion, localization of actin-related molecules, and validation data from multiple inhibitor experiments are clear.

Weaknesses:

This study does not include any assessment of whether the two types of endosome fusions claimed by the authors occur in general cells, so the article is limited to showing a phenomenon specific to yolk sac lateral endoderm cells. Also, the study does not show the physiological importance of the two types of fusion. There are some unclear points in the method of image analysis and some of the descriptions in the text are not logical.

eLife assessment

This study presents valuable findings on two distinct modes of endosomal fusion and the roles of actin dynamics in this process. The evidence supporting the authors' claims is solid, although the underlying molecular mechanisms and whether the proposed fusion modes are applicable in other cell types remain unclear. The work will be of interest to cell biologists and biophysicists working on the cytoskeleton and organelles.

Reviewer #1 (Public Review):

Summary:

This manuscript employs yolk sac visceral endoderm cells as a novel model for studying endosomal fusion, observing two distinct fusion behaviors: quick homotypic fusion between late endosomes, and slower heterotypic fusion between late endosomes and lysosomes. The mathematical modeling suggests that vesicle size critically influences the mode of fusion. Further investigations reveal that actin filaments are dynamically associated with late endosomal membranes, and are oriented in the x-y plane and along the apical-basal axis. Actin and Arf2/3 were shown to appear at the rear end of the endosomes along the moving direction suggesting polymerization of actin may provide force for the movement of endosomes. Additionally, the authors found that actin dynamics regulate homotypic and heterotypic fusion events in a different manner. The authors also provide evidence to suggest that Cofilin-dependent actin dynamics are involved in late endosome fusion.

Strengths:

The unique feature of this study is that the authors use yolk sac visceral endoderm cells to study endosomal fusion. Yolk sac visceral endoderm cells have huge endocytic vesicles, endosomes, and lysosomes, offering an excellent system to explore endosomal fusion dynamics and the assembly of cellular factors on membranes. The manuscript provides a valuable and convincing observation of the modes of endosomal fusion and the roles of actin dynamics in this process, and the conclusions of the study are justified by the data.

Weaknesses:

While the study offers compelling observations, it falls short of delivering clear mechanistic insights. Key questions remain unaddressed, such as the functional significance of actin filaments that extend apically in positioning late endosomes, the ways in which actin dynamics influence fusion events, and the functional implications of the slower bridge fusion process.

Reviewer #2 (Public Review):

Summary:

Seiichi Koike et al. studied two fusion models, explosive fusion, and bridge fusion, utilizing yolk sac visceral endoderm cells. They elucidated these two fusion models in vivo by employing mathematical modeling and incorporating fluctuations derived from actin dynamics as a key regulator for rapid homotypic fusion between late endosomes.

Strengths:

This study uncovered the role of actin dynamics in regulating the transition of fusion models in homotypic fusion between late endosomes and introduced a method for observing the fusion of single vesicles with two different targets. The role of actin dynamics in vesicle fusion in other systems has been extensively studied. This study could offer useful insights for research on vesicle fusion.

Weaknesses:<br /> The physiological significance of different fusion models is lacking.

Joint Public Review:

The present study focuses on the structure and function of human PURA, a regulator of gene transcription and mRNA transport and translation whose mutation causes the neurodevelopmental PURA syndrome, characterized by developmental delay, intellectual disability, hypotonia, epileptic seizures, a.o. deficits. The authors combined structural biology, molecular dynamics simulation, and various cell biological assays to study the effects of disease-causing PURA mutations on protein structure and function. The corresponding data reveal a highly dynamic PURA structure and show that disease-related mutations in PURA cause complex defects in folding, DNA-unwinding activity, RNA binding, dimerization, and partitioning into processing bodies. These findings provide first insights into how very diverse PURA mutations can cause penetrant molecular, cellular, and clinical defects. This will be of substantial interest to cell biologists, neurogeneticists, and neurologists alike.

A particular strength of the present study is the structural characterization of human PURA, which is a challenging target for structural biology approaches. The molecular dynamics simulations are state-of-the-art, allowing a statistically meaningful assessment of the differences between wild-type and mutant proteins. The functional consequences of PURA mutations at the cellular level are fascinating, particularly the differential compartmentalization of wild-type and mutant PURA variants into certain subcellular condensates.

eLife assessment

This important study addresses the mechanisms by which mutations in the PURA protein, a regulator of gene transcription and mRNA transport and translation, cause the neurodevelopmental PURA syndrome. Based on convincing evidence from structural biology, molecular dynamics simulation, biochemical, and cell biological analyses, the authors show that the PURA structure is very dynamic, rendering it generally sensitive to structure-altering mutations that affect its folding, DNA-unwinding activity, RNA binding, dimerization, and partitioning into processing bodies. These findings are of substantial importance to cell biology, neurogenetics, and neurology alike, because they provide first insights into how very diverse PURA mutations can cause similar and penetrant molecular, cellular, and clinical defects.

eLife assessment

This useful study describes expression profiling by scRNA-seq of thousands of cells of recombinant yeast genotypes from a system that models natural genetic variation. The rigorous new method presented here holds promise for improving the efficiency of genotype-to-phenotype mapping in yeast, providing convincing evidence for its efficacy. This manuscript focuses on overcoming technical challenges with this approach. It currently offers somewhat limited new biological insights to place the work within the broader context of the field. Doing so would broaden the interest of the work for all geneticists and evolutionary biologists.

Reviewer #1 (Public Review):

In this paper, N'Guessan et al report a study of expression QTL (eQTL) mapping in yeast using single cells. The authors make use of advances in single-cell RNAseq (scRNAseq) in yeast to increase the efficiency with which this type of analysis can be undertaken. Building on prior research led by the senior author that entailed genotyping and fitness profiling of almost 100,000 cells derived from a cross between two yeast strains (BY and RM) they performed scRNAseq on a subset of 4,489 individual cells. To address the sparsity of genotype data in the expression profiling they used a Hidden Markov Model (HMM) to infer genotypes and then identify the most likely known lineage genotype from the original dataset. To address the relationship between variance in fitness and gene expression the authors partition the variance to investigate the sources of variation. They then perform eQTL mapping and study the relationship between eQTL and fitness QTL identified in the earlier study.

This paper seeks to address the challenging question of how quantitative trait variation and expression variation are related. scRNAseq represents an appealing approach to eQTL mapping as it is possible to simultaneously genotype individual cells and measure expression in the same cell. As eQTL mapping requires large sample sizes to identify statistical relationships, this approach is likely to dramatically increase the statistical power of such studies. However, there are several technical challenges associated with scRNAseq and the authors' study is focused on addressing those challenges. Although the authors present results suggesting the feasibility of the approach there are limitations in the conclusions that can be drawn in the current study owing to the lack of clarity in the presentation of the results. Ultimately, this study presents a proof of concept with limited novel biological insights that would nonetheless make a useful contribution to the literature if the following major points were addressed:

(1) There is insufficient information provided about the nature of data. At a minimum, the following information should be provided to enable assessment of the study: What is the total library size, how many genes are identified per cell, how many UMIs are found per cell, what is the doublet rate, and how are doublets identified (e.g. on the basis of heterozygous calls at polymorphic loci?), how many times is each genotype observed, and how many polymorphic sites are identified per cell that are the basis of genotype inferences?

(2) The prior study analyzed 18 different conditions, whereas this study only assays expression in a single condition. However, the power of the authors' approach is that its efficiency enables testing eQTLs in multiple conditions. The study would be greatly strengthened through analysis of at least one more condition, and ideally several more conditions. The previous fitness study would be a useful guide for choosing additional conditions as identifying those conditions that result in the greatest contrasts in fitness QTL would be best suited to testing the generalizations that can be drawn from the study.

(3) Alternatively, the authors could demonstrate the power of their approach by applying it to a cross between two other yeast strains. As the cross between BY and RM has been exhaustively studied, applying this approach to a different cross would increase the likelihood of making novel biological discoveries.

(4) Figure 1 is misleading as A presents the original study from 2022 without important details such as how genotypes were identified. It is unclear what the barcode is in this study and how it is used in the analysis. Is the barcode for each lineage transcribed so that it is identified in the scRNAseq data? Or, does the barcode in B refer to the cell index barcode? A clearer presentation and explanation of terms are needed to understand the method.

(5) The rationale for the analysis reported in Figure 2B is unclear. The fitness data are from the previous study and the goal is to estimate the heritability using the genotyping data from the scRNAseq data. What is the explanation for why the data don't agree for only one condition, i.e. 37C? And, what are we to understand from the overall result?

(6) Figure 3 presents an analysis of variance partitioning as a Venn diagram. This summarized result is very hard to understand in the absence of any examples of what the underlying raw data look like. For example, what does trait variation look like if only genotype explains the variance or if only gene expression explains the variance? The presented highly summarized data is not intuitive and its presentation is poor - the result that is currently provided would be easier to read in a table format, but the reader needs more information to be able to interpret and understand the result.

(7) I am concerned about the conclusions that can be drawn about expression heritability. The authors claim that expression heritability is correlated with expression levels. It seems likely that this reflects differing statistical power. How can this possibility be excluded?

(8) Conversely, the authors claim that the genes with the lowest heritability are genes involved in the cell cycle. However, uniquely in scRNAseq, cell cycle regulated genes appear to have the highest variance in the data as they are only expressed in a subset of cells. Without incorporating this fact one would erroneously conclude that the variation is not heritable. To test the heritability of cell cycle regulation genes the authors should partition the cells into each cell cycle stage based on expression.

(9) I do not understand Figure S5 and how eQTL sites are assigned to these specific classes given that the authors say that causative variation cannot be resolved because of linkage disequilibrium.

(10) The paragraph starting at line 305 is very confusing. In particular, the authors state that they identify a hotspot of regulation at the mating type locus. It is not obvious why this would be the case. Moreover, they claim that they find evidence for both MATa and MATalpha gene expression. Information is not provided about how segregants were isolated, but assuming that the authors did not dissect 25,000 tetrads to obtain 100,000 segregants I would infer that random spore using SGA was used. In that case, all cells should be MATa. The authors should clarify and explain this observation.

(11) Ultimately, it is not clear what new biological findings the authors have made. There are no novel findings with respect to causative variation underlying eQTLs and I would encourage the authors to make clearer statements in their abstract, introduction, and conclusion about the key discoveries. E.g. What are the "new associations between phenotypic and transcriptomic variations" mentioned in the abstract?

The following minor points should be addressed:

(1) The segregants should be referred to as F2 segregants as they are derived from an F1 cross.

(2) The connections to eQTLs in other organisms should be addressed in the introduction and conclusion. For example, in humans, there has been little evidence for trans eQTLs in contrast to what has been found in yeast.

(3) The authors state that an advantage of scRNAseq over bulk is that it captures rare cell populations (line 79), but this advantage is not exploited in this study.

(4) The authors use ~5% of the lineages from the original study. There is no rationale for why this is an appropriate sample size. Is there an argument for using more cells in eQTL mapping or conversely could the authors ask if fewer cells would provide similar conclusions by downsampling?

(5) I do not agree that the use of UMIs overcomes the challenges of low sequencing depth. UMIs mitigate the possible technical artifacts due to massive PCR amplification.

(6) There is an inadequate reference to prior work on scRNAseq in yeast that established the methods used by the authors and eQTL mapping in human cells using scRNAseq.

(7) The use of empty quotes in Figure 4A is confusing and an alternative presentation method should be used.

(8) The authors speculate about the use of predicted fitness instead of observed fitness, but this is something they could explicitly address in their current study.

Reviewer #2 (Public Review):

Summary:

The experiments and analysis appear to be carefully done. My concerns center on the impact of the work in its current form on the research community.

The focal yeast cross here has been the subject of many previous publications (for smaller sets of recombinant progeny), by the last author and others, including phenotyping, genotyping, transcriptomics, and proteomics. This mini-literature has proven relevant to the community because it has empirically pinpointed exactly how many variants underlie a given trait, both molecular and cellular. That is, whereas in more complex organisms we try our best to estimate/infer the full genetic architecture of varying traits from the results of mapping of necessarily weaker power, the highly-powered yeast system can access a more comprehensive mapping of the dozens of loci impinging on a given trait and learn from it. The question is what exactly we learn from the current study?

Strengths and weaknesses:

Most of the figures center on methods development and validation for the authors' single-cell RNA-seq in the yeast cross, including generating the large raw data set; analysis pipelines for mapping and genotyping (Figure 1); and higher-level analyses that recapitulate previously reported trends in heritability (Figure 2) and eQTL mapping (Figure 3 and Figure 4B-C). One potential novelty of the study is the methods per se: that is, showing that scRNA-seq works for concomitant genotyping and gene expression profiling in the natural variation context. The authors' rigor and effort notwithstanding: in my view, this can be described as modest in terms of principles. That is, the authors did a good job putting the scRNA-seq idea into practice, but their success is perhaps not surprising or highly relevant for work outside of yeast (as the discussion says). The more substantive claim by the authors for the impact of the study is that they make new observations about the role of expression in phenotype (lines 333-335). The major display item of the manuscript on this theme is Figure 4A, reporting which loci that control growth phenotype (from an earlier paper) also control expression. This is solid but I regret to say that the results strike me as modest. The discussion makes some perhaps fairly big claims that the work has helped "bridge understanding of how genetic variation influences transcriptomic variation" and ultimately cellular phenotype. But with the data as they stand, the authors have missed an opportunity to crystallize exactly how a given variant affects expression (perhaps in waves of regulators affecting targets that affect more regulators) and then phenotype, except for the speculations in the text on lines 305-319. The field started down this road years ago with Bayesian causality inference methods applied to eQTL and phenotype mapping (via e.g. the work of Eric Schadt). The authors could now try Mendelian randomization-type fine-grained detailed models for more firepower toward the same end, and/or experimental tests of the genotype-to-expression-to-phenotype relationship. I would see these directions, motivated by fundamental questions that are relevant to the field at large, as leading to a major advance for this very crowded field. As it stands, I felt their absence in this manuscript especially if the authors are selling principles about linking expression and phenotype as their take-home. I also wonder whether the co-mapping of expression and growth traits in Figure 4A would have been possible with e.g. the bulk RNA-seq from Albert et al., 2018, and I recommend that the authors repeat the Figure 4A-type analyses with the latter to justify their statement that their massive scRNA data set would actually be necessary for them to bear fruit (lines 386-388).

I also read the discussion of the manuscript as bringing to the fore some of the challenges a reader has in judging the current state of the results to be of actionable impact. The discussion, and the manuscript, will be improved if the authors can put the work in context, posing concrete questions from the field and stating how they are addressed here and what's left to do.

eLife assessment

This important study used Voltage Sensitive Dye Imaging (VSDI) to measure neural activity in the primary visual cortex of monkeys trained to detect an oriented grating target that was presented either alone or against an oriented mask. The authors show convincingly that the initial effect of the mask ran counter to the behavioral effects of the mask, a pattern that reversed in the latter phase of the response. They interpret these results in terms of influences from the receptive field center, and although an alternative view that emphasizes the role of the receptive field surround also seems reasonable, this study stands as an interesting contribution to our understanding of mechanisms of visual perception.

Reviewer #1 (Public Review):

Summary:

The manuscript describes the crystal structures of Streptococcus pneumoniae NOXs. Crystals were obtained for the wild-type and mutant dehydrogenase domain, as well as for the full-length protein comprising the membrane domain. The manuscript further carefully studies the enzyme's kinetics and substrate-specificity properties. Streptococcus pneumoniae NOX is a non-regulated enzyme, and therefore, its structure should provide a view of the NOX active conformation. The structural and biochemical data are discussed on this ground.

Strengths:

This is very solid work. The protein chemistry and biochemical analysis are well executed and carefully described. Similarly, the crystallography must be appreciated given the difficulty of obtaining good enzyme preparations and the flexibility of the protein. Even if solved at medium resolution, the crystal structure of the full-length protein conveys relevant information. The manuscript nicely shows that the domain rotations are unlikely to be the main mechanistic element of NOX regulation. It rather appears that the NADPH-binding conformation is pivotal to enzyme activation. The paper extensively refers to the previous literature and analyses the structures comprehensively with a comparison to previously reported structures of eukaryotic and prokaryotic NOXs.

Reviewer #2 (Public Review):

The authors describe the structure of the S. pneumoniae Nox protein (SpNOX). This is a first. The relevance of it to the structure and function of eukaryotic Noxes is discussed in depth.

One of the strengths of this work is the effort put into preparing a pure and functionally active SpNOX preparation. The protein was expressed in E. coli and the purification and optimization of its thermostability and activity are described in detail, involving salt concentration, glycerol concentration, and pH.

Comments on revised version:

This reviewer would like to compliment the authors for the conscientious revision of the manuscript. Their response to the comments and the detailed explanations of the issues that did not appear clear enough to the reviewer are much appreciated. Their reaction to the review was not only superbly competent but also prominently good natured.

The revised version is perfect and represents a major contribution to our understanding of the molecular details of Nox function. As for the questions not yet answered, I shall quote the authors: "Time will tell".

eLife assessment

In this manuscript, the authors investigate the properties of prokaryotic NADPH oxidases (NOX) and discuss the implications for NOX regulation and function. The structure of the S. pneumoniae Nox protein is an important step forward in our understanding of procaryotic NOX enzymes and the characterization and interpretation are convincing. The results will be of interest to structural biologists as well as biochemists focusing on enzymatic functions.

eLife assessment

This important study identifies the gene mamo as a new regulator of pigmentation in the silkworm Bombyx mori, a function that was previously unsuspected based on extensive work on Drosophila where the mamo gene is involved in gamete production. The evidence supporting the role of Bm-nano in pigmentation is convincing, including high-resolution linkage mapping of two mutant strains, expression profiling, and reproduction of the mutant phenotypes with state-of-the-art RNAi and CRISPR knock-out assays. The work will be of interest to evolutionary biologists and geneticists studying color patterns and evolution of gene networks.

Author Response

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

Public Reviews:

Reviewer #2 (Public Review):

I would like to express my appreciation for the authors' dedication to revising the manuscript. It is evident that they have thoughtfully addressed numerous concerns I previously raised, significantly contributing to the overall improvement of the manuscript.

Response: We appreciate the reviewers’ recognition of our efforts in revising the manuscript.

My primary concern regarding the authors' framing of their findings within the realm of habitual and goal-directed action control persists. I will try explain my point of view and perhaps clarify my concerns. While acknowledging the historical tendency to equate procedural learning with habits, I believe a consensus has gradually emerged among scientists, recognizing a meaningful distinction between habits and skills or procedural learning. I think this distinction is crucial for a comprehensive understanding of human action control. While these constructs share similarities, they should not be used interchangeably. Procedural learning and motor skills can manifest either through intentional and planned actions (i.e., goal-directed) or autonomously and involuntarily (habitual responses).

Response: We would like to clarify that, contrary to the reviewer’s assertion of a scientific consensus on this matter, the discussion surrounding the similarities and differences between habits and skills remains an ongoing and unresolved topic of interest among scientists (Balleine and Dezfouli, 2019; Du and Haith, 2023; Graybiel and Grafton, 2015; Haith and Krakauer, 2018; Hardwick et al., 2019; Kruglanski and Szumowska, 2020; Robbins and Costa, 2017). We absolutely agree with the reviewer that “Procedural learning and motor skills can manifest either through intentional and planned actions (i.e., goal-directed) or autonomously and involuntarily (habitual responses)”. But so do habits. Some researchers also highlight the intentional/goal-directed nature of habits (e.g., Du and Haith, 2023, “Habits are not automatic” (preprint) or Kruglanski and Szumowska, 2020, “Habitual behavior is goal-driven”: “definitions of habits that include goal independence as a foundational attribute of habits are begging the question; they effectively define away, and hence dispose of, the issue of whether habits are goal-driven (p 1258).” Therefore, there is no clear consensus concerning the concept of habit.

While we acknowledge the meaningful distinctions between habits and skills, we also recognize a substantial body of literature supporting the overlap between these concepts (cited in our manuscript), particularly at the neural level. The literature clearly indicates that both habits and skills are mediated by subcortical circuits, with a progressive disengagement of cognitive control hubs in frontal and cingulate cortices as repetition evolves. We do not use these concepts interchangeably. Instead, we simply present evidence supporting the assertion that our trained app sequences meet several criteria for their habitual nature.

Our choice of Balleine and Dezfouli (2018)'s criteria stemmed from the comprehensive nature of their definitions, which effectively synthesized insights from various researchers (Mazar and Wood, 2018; Verplanken et al., 1998; Wood, 2017, etc). Importantly, their list highlights the positive features of habits that were previously overlooked. However, these authors still included a controversial criterion ("habits as insensitive to changes in their relationship to their individual consequences and the value of those consequences"), even though they acknowledged the problems of using outcome devaluation methods and of relying on a null-effect. According to Kruglanski and Szumowska (2020), this criterion is highly problematic as “If, by definition, habits are goalindependent, then any behavior found to be goal-dependent could not be a habit on sheer logical grounds” (p. 1257). In their definition, “habitual behavior is sensitive to the value of the reward (i.e., the goal) it is expected to mediate and is sensitive to the expectancy of goal attainment (i.e., obtainment of the reward via the behavior, p.1265). In fact, some recent analyses of habitual behavior are not using devaluation or revaluation as a criterion (Du and Haith, 2023). This article, for example, ascertains habits using different criteria and provides supporting evidence for trained action sequences being understood as skills, with both goal-directed and habitual components.

In the discussion of our manuscript, we explicitly acknowledge that the app sequences can be considered habitual or goal-directed in nature and that this terminology does not alter the fact that our overtrained sequences exhibit clear habitual features.

Watson et al. (2022) aptly detailed my concerns in the following statements: "Defining habits as fluid and quickly deployed movement sequences overlaps with definitions of skills and procedural learning, which are seen by associative learning theorists as different behaviors and fields of research, distinct from habits."

"...the risk of calling any fluid behavioral repertoire 'habit' is that clarity on what exactly is under investigation and what associative structure underpins the behavior may be lost." I strongly encourage the authors, at the very least, to consider Watson et al.'s (2022) suggestion: "Clearer terminology as to the type of habit under investigation may be required by researchers to ensure that others can assess at a glance what exactly is under investigation (e.g., devaluationinsensitive habits vs. procedural habits)", and to refine their terminology accordingly (to make this distinction clear). I believe adopting clearer terminology in these respects would enhance the positioning of this work within the relevant knowledge landscape and facilitate future investigations in the field.

Response: We would like to highlight that we have indeed followed Watson et al (2022)’s recommendations on focusing on other features/criteria of habits at the expense of the outcome devaluation/contingency degradation paradigm, which has been more controversial in the human literature. Our manuscript clearly aligns with Watson et al. (2022) ‘s recommendations: “there are many other features of habits that are not captured by the key metrics from outcome devaluation/contingency degradation paradigms such as the speed at which actions are performed and the refined and invariant characteristics of movement sequences (Balleine and Dezfouli, 2019). Attempts are being made to develop novel behavioral tasks that tap into these positive features of habits, and this should be encouraged as should be tasks that are not designed to assess whether that behavior is sensitive to outcome devaluation, but capture the definition of habits through other measures”.

Regarding the authors' use of Balleine and Dezfouli's (2018) criteria to frame recorded behavior as habitual, as well as to acknowledgment the study's limitations, it's important to highlight that while the authors labelled the fourth criterion (which they were not fulfilling) as "resistance to devaluation," Balleine and Dezfouli (2018) define it as "insensitive to changes in their relationship to their individual consequences and the value of those consequences." In my understanding, this definition is potentially aligned with the authors' re-evaluation test, namely, it is conceptually adequate for evaluating the fourth criterion (which is the most accepted in the field and probably the one that differentiate habits from skills). Notably, during this test, participants exhibited goaldirected behavior.

The authors characterized this test as possibly assessing arbitration between goal-directed and habitual behavior, stating that participants in both groups "demonstrated the ability to arbitrate between prior automatic actions and new goal-directed ones." In my perspective, there is no justification for calling it a test of arbitration. Notably, the authors inferred that participants were habitual before the test based on some criteria, but then transitioned to goal-directed behavior based on a different criterion. While I agree with the authors' comment that: "Whether the initiation of the trained motor sequences in experiment 3 (arbitration) is underpinned by an action-outcome association (or not) has no bearing on whether those sequences were under stimulus-response control after training (experiment 1)." they implicitly assert a shift from habit to goal-directed behavior without providing evidence that relies on the same probed mechanism. Therefore, I think it would be more cautious to refer to this test as solely an outcome revaluation test. Again, the results of this test, if anything, provide evidence that the fourth criterion was tested but not met, suggesting participants have not become habitual (or at least undermines this option).

Response: In our previously revised manuscript, we duly acknowledged that the conventional (perhaps nowadays considered outdated) goal devaluation criterion was not met, primarily due to constraints in designing the second part of the study. We did cite evidence from another similar study that had used devaluation app-trained action sequences to demonstrate habitual qualities (but the reviewer ignored this).

The reviewer points out that we did use a manipulation of goal revaluation in one of the follow-up tests conducted (although this was not a conventional goal revaluation test inasmuch that it was conducted in a novel context). In this test, please note that we used 2 manipulations: monetary and physical effort. Although we did show that subjects, including OCD patients, were apparently goaldirected in the monetary reward manipulation, this was not so clear when goal re-evaluation involved the physical effort expended. In this effort manipulation, participants were less goaloriented and OCD patients preferred to perform the longer, familiar, to the shorter, novel sequence, thus exhibiting significantly greater habitual tendencies, as compared to controls. Hence, we cannot decisively conclude that the action sequence is goal-directed as the reviewer is arguing. In fact, the evidence is equivocal and may reflect both habitual and goal-directed qualities in the performance of this sequence, consistent with recent interpretations of skilled/habitual sequences (Du and Haith, 2023). Relying solely on this partially met criterion to conclude that the app-trained sequences are goal-directed, and therefore not habitual, would be an inaccurate assessment for several reasons: 1) the action sequences did satisfy all other criteria for being habitual; 2) this approach would rest on a problematic foundation for defining habits, as emphasized by Kruglanski & Szumowska (2020); and 3) it would succumb to the pitfall of subscribing to a zero-sum game perspective, as cautioned by various researchers, including the review by Watson et al. (2022) cited by the referee, thus oversimplifying the nuanced nature of human behavior.

While we have previously complied with the reviewer’s suggestion on relabelling our follow-up test as a “revaluation test” instead of an “arbitration test”, we have now explicitly removed all mentions of the term “arbitration” (which seems to raise concerns) throughout the manuscript. As the reviewer has suggested, we now use a more refined terminology by explicitly referring to the measured behavior as "procedural habits", as he/she suggested. We have also extensively revised the discussion section of our manuscript to incorporate the reviewer’s viewpoint. We hope that these adjustments enhance the clarity and accuracy of our manuscript, addressing the concerns raised during this review process.

In essence, this is an ontological and semantic matter, that does not alter our findings in any way. Whether the sequences are consider habitual or goal directed, does not change our findings that 1) Both groups displayed equivalent procedural learning and automaticity attainment; 2) OCD patients exhibit greater subjective habitual tendencies via self-reported questionnaires; 3) Patients who had elevated compulsivity and habitual self-reported tendencies engaged significantly more with the motor habit-training app, practiced more and reported symptom relief at the end of the study; 4) these particular patients also show an augmented inclination to attribute higher intrinsic value to familiar actions, a possible mechanism underlying compulsions.

Reviewer #2 (Recommendations For The Authors):

A few more small comments (with reference to the point numbers indicated in the rebuttal):

(14) I am not entirely sure why the suggested analysis is deemed impractical (i.e., why it cannot be performed by "pretending" participants received the points they should have received according to their performance). This can further support (or undermine) the idea of effect of reward on performance rather than just performance on performance.

Response: We have now conducted this analysis, generating scores for each trial of practices after day 20, when participants no longer gained points for their performance. This analysis assesses whether participants trial-wise behavioral changes exhibit a similar pattern following simulated relative increases or decrease in scores, as if they had been receiving points at this stage. Note that this analysis has fewer trials available, around 50% less on average.

Before presenting our results, we wish to emphasize the importance of distinguishing between the effects of performance on performance and the effects of reward on performance. In response to a reviewer's suggestion, we assessed the former in the first revision of our manuscript. We normalized the movement time variable and evaluated how normalized behavioral changes responded to score increments and decrements. The results from the original analyses were consistent with those from the normalized data.

Regarding the phase where participants no longer received scores, we believe this phase primarily helps us understand the impact of 'predicted' or 'learned' rewards on performance. Once participants have learned the simple association between faster performance and larger scores, they can be expected to continue exhibiting the reward sensitivity effects described in our main analysis. We consider it is not feasible to assess the effects of performance on performance during the reward removal phase, which occurs after 20 days. Therefore, the following results pertain to how the learned associations between faster movement times and scores persist in influencing behavior, even when explicit scores are no longer displayed on the screen.

Results: The main results of the effect of reward on behavioral changes persist, supporting that relative increases or decreases in scores (real or imagined/inferred) modulate behavioral adaptations trial-by-trial in a consistent manner across both cohorts. The direction of the effects of reward is the same as in the main analyses presented in the manuscript: larger mean behavioral changes (smaller std) following ∆R- . First, concerning changes in “normalized” movement time (MT) trial-by-trial, we conducted a 2 x 2 factorial analysis of the centroid of the Gaussian distributions with the same factors Reward, Group and Bin. This analysis demonstrated a significant main effect of Reward (P = 2e-16), but not of Group (P = 0.974) or Bin (P = 0.281). There were no significant interactions between factors. The main Reward effect can be observed in the top panel of the figure below. The same analysis applied to the spread (std) of the Gaussian distributions revealed a significant main effect of Reward (P = 0.000213), with no additional main effects or interactions.

Author response image 1.

Next, conducting the same 2 x 2 factorial analyses on the centroid and spread of the Gaussian distributions fitted to the Consistency data, we also obtained a robust significant main effect of Reward. For the centroid variable, we obtained a significant main effect of Reward (P = 0.0109) and Group (P = 0.0294), while Bin and the factor interactions were non-significant. See the top panel of the figure below.

On the other hand, Reward also modulated significantly the spread of the Gaussian distributions fitted to the Consistency data, P = 0.00498. There were no additional significant main effects or interactions. See the bottom panel in the figure below.

Note that here the factorial analysis was performed on the logarithmic transformation of the std.

Author response image 2.

(16) I find this result interesting and I think it might be worthwhile to include it in the paper.

Response: We have now included this result in our revised manuscript (page 28)

(18) I referred to this sentence: "The app preferred sequence was their preferred putative habitual sequence while the 'any 6' or 'any 3'-move sequences were the goal-seeking sequences." In my understanding, this implies one choice is habitual and another indicates goal-directedness.

One last small comment:
In the Discussion it is stated: "Moreover, when faced with a choice between the familiar and a new, less effort-demanding sequence, the OCD group leaned toward the former, likely due to its inherent value. These insights align with the theory of goal-direction/habit imbalance in OCD (Gillan et al., 2016), underscoring the dominance of habits in particular settings where they might hold intrinsic value."

This could equally be interpreted as goal-directed behavior, so I do not think there is conclusive support for this claim.

Response: The choice of the familiar/trained sequence, as opposed to the 'any 6' or 'any 3'-move sequences cannot be explicitly considered goal-directed: firstly, because the app familiar sequences were associated with less monetary reward (in the any-6 condition), and secondly, because participants would clearly need more effort and time to perform them. Even though these were automatic, it would still be much easier and faster to simply tap one finger sequentially 6 times (any6) or 3 times (any-3). Therefore, the choice for the app-sequence would not be optimal/goaldirected. In this sense, that choice aligns with the current theory of goal-direction/habit imbalance of OCD. We found that OCD patients prefer to perform the trained app sequences in the physical effort manipulation (any-3 condition). While this, on one hand cannot be explicitly considered a goal-directed choice, we agree that there is another possible goal involved here, which links to the intrinsic value associated to the familiar sequence. In this sense the action could potentially be considered goal-directed. This highlights the difficulty of this concept of value and agrees with: 1) Hommel and Wiers (2017): “Human behavior is commonly not driven by one but by many overlapping motives . . . and actions are commonly embedded into larger-scale activities with multiple goals defined at different levels. As a consequence, even successful satiation of one goal or motive is unlikely to also eliminate all the others(p. 942) and 2) Kruglanski & Szumowska (2020)’s account that “habits that may be unwanted from the perspective of an outsider and hence “irrational” or purposeless, may be highly wanted from the perspective of the individual for whom a habit is functional in achieving some goal” (p. 1262) and therefore habits are goal-driven.

References:

Balleine BW, Dezfouli A. 2019. Hierarchical Action Control: Adaptive Collaboration Between Actions and Habits. Front Psychol 10:2735. doi:10.3389/fpsyg.2019.02735

Du Y, Haith A. 2023. Habits are not automatic. doi:10.31234/osf.io/gncsf Graybiel AM, Grafton ST. 2015. The Striatum: Where Skills and Habits Meet. Cold Spring Harb Perspect Biol 7:a021691. doi:10.1101/cshperspect.a021691

Haith AM, Krakauer JW. 2018. The multiple effects of practice: skill, habit and reduced cognitive load. Current Opinion in Behavioral Sciences 20:196–201. doi:10.1016/j.cobeha.2018.01.015

Hardwick RM, Forrence AD, Krakauer JW, Haith AM. 2019. Time-dependent competition between goal-directed and habitual response preparation. Nat Hum Behav 1–11. doi:10.1038/s41562019-0725-0

Hommel B, Wiers RW. 2017. Towards a Unitary Approach to Human Action Control. Trends Cogn Sci 21:940–949. doi:10.1016/j.tics.2017.09.009

Kruglanski AW, Szumowska E. 2020. Habitual Behavior Is Goal-Driven. Perspect Psychol Sci 15:1256– 1271. doi:10.1177/1745691620917676

Mazar A, Wood W. 2018. Defining Habit in Psychology In: Verplanken B, editor. The Psychology of Habit: Theory, Mechanisms, Change, and Contexts. Cham: Springer International Publishing. pp. 13–29. doi:10.1007/978-3-319-97529-0_2

Robbins TW, Costa RM. 2017. Habits. Current Biology 27:R1200–R1206. doi:10.1016/j.cub.2017.09.060

Verplanken B, Aarts H, van Knippenberg A, Moonen A. 1998. Habit versus planned behaviour: a field experiment. Br J Soc Psychol 37 ( Pt 1):111–128. doi:10.1111/j.2044-8309.1998.tb01160.x

Watson P, O’Callaghan C, Perkes I, Bradfield L, Turner K. 2022. Making habits measurable beyond what they are not: A focus on associative dual-process models. Neurosci Biobehav Rev 142:104869. doi:10.1016/j.neubiorev.2022.104869

Wood W. 2017. Habit in Personality and Social Psychology. Pers Soc Psychol Rev 21:389–403. doi:10.1177/1088868317720362

eLife assessment

This study provides solid evidence for differences in habit-learning in obsessive-compulsive disorder versus controls. Contrary to previous studies that employed a single laboratory session to study habit-learning, here a smartphone app delivered motor-sequence tasks daily for a month. These results have important implications for our understanding of goal-directed versus habit learning in obsessive-compulsive disorder.

Reviewer #1 (Public Review):

It is known that aberrant habit formation is a characteristic of obsessive-compulsive disorder (OCD). Habits can be defined according to the following features (Balleine and Dezfouli, 2019): rapid execution, invariant response topography, action 'chunking' and resistance to devaluation.

The extent to which OCD behavior is derived from enhanced habit formation relative to deficits in goal-directed behavior is a topic of debate in the current literature. This study examined habit-learning specifically (cf. deficits in goal-directed behavior) by regularly presenting, via smartphone, sequential learning tasks to patients with OCD and healthy controls. Participants engaged in the tasks every day over the course of a month. Automaticity, including the extent to which individual actions in the sequence become part of a unified 'chunk', was an important outcome variable. Following the 30 days of training, in-laboratory tasks were then administered to examine 1) if performing the learned sequences themselves had become rewarding 2) differences in goal-directed vs. habitual behavior.

Several hypotheses were tested, including:<br /> Patients would have impaired procedural learning vs. healthy volunteers (this was not supported, possibly because there were fewer demands on memory in the task used here)<br /> Once the task had been learned, patients would display automaticity faster (unexpectedly, patients were slower to display automaticity)<br /> Habits would form faster under a continuous (vs. variable) reinforcement schedule

Exploratory analyses were also conducted: an interesting finding was that OCD patients with higher self-reported symptoms voluntarily completed more sessions with the habit-training app and reported a reduction in symptoms.

Strengths

This paper is well situated theoretically within the habit learning/OCD literature.<br /> Daily training in a motor-learning task, delivered via smartphone, was innovative, ecologically valid and more likely to assay habitual behaviors specifically. Daily training is also more similar to studies with non-humans, making a better link with that literature. The use of a sequential-learning task (cf. tasks that require a single response) is also more ecologically valid.<br /> The in-laboratory tests (after the 1 month of training) allowed the researchers to test if the OCD group preferred familiar, but more difficult, sequences over newer, simpler sequences.

Weaknesses

The authors were not able to test one criterion of habits, namely resistance to devaluation, due to the nature of the task.<br /> The sample size was relatively small. Some potentially interesting individual differences within the OCD group could have been examined more thoroughly with a bigger sample (e.g., preference for familiar sequences). A larger sample may have allowed the statistical testing of any effects due to medication status.

The authors achieved their aims in that two groups of participants (patients with OCD and controls) engaged with the task over the course of 30 days. The repeated nature of the task meant that 'overtraining' was almost certainly established, and automaticity was demonstrated. This allowed the authors to test their hypotheses about habit learning. The results are supportive of the author's conclusions.

This article is likely to be impactful -- the delivery of a task across 30 days to a patient group is innovative and represents a new approach for the study of habit learning that is superior to an in-laboratory approach.

An interesting aspect of this manuscript is that it prompts a comparison with previous studies of goal-directed/habitual responding in OCD that used devaluation protocols, and which may have had their effects due to deficits in goal-directed behavior and not enhanced habit learning per se.

Author Response

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

eLife assessment

This manuscript represents a cleanly designed experiment for assessing biological motion processing in children (mean age = 9) with and without ADHD. The group differences concerning accuracy in global and local motion processing abilities are solid, but the analyses suggesting dissociable relationships between global and local processing and social skills, age, and IQ need further interrogation. The results are useful in terms of understanding ADHD and the ontogenesis of different components of the processing of biological motion.

We thank the editors for the positive assessment of our manuscript. We have carefully considered the reviewers’ constructive and helpful comments and revised our manuscript accordingly. To address the question about the dissociable relationships between global and local BM processing, we have provided more evidence and additional analyses in this revised version.

Reviewer #1 (Public Review):

Summary:

The paper presents a nice study investigating differences in biological motion perception in participants with ADHD in comparison with controls. Motivated by the idea that there is a relationship between biological motion perception and social capabilities, the authors investigated local and global (holistic) biological motion perception, the group, and several additional behavioral variables that are affected in ADHS (IQ, social responsiveness, and attention/impulsivity). As well as local global biological motion perception is reduced in ADHD participants. In addition, the study demonstrates a significant correlation between local biological motion perception skills and the social responsiveness score in the ADHD group, but not the controls. A path analysis in the ADHD data suggests that general performance in biological motion perception is influenced mainly by global biological motion perception performance and attentional and perceptual reasoning skills.

Strengths:

It is true that there exists not much work on biological motion perception and ADHD. Therefore, the presented study contributes an interesting new result to the biological motion literature and adds potentially also new behavioral markers for this clinical condition. The design of the study is straightforward and technically sound, and the drawn conclusions are supported by the presented results.

Thank you for your positive assessment of our work.

Weaknesses:

Some of the claims about the relationship between genetic factors and ADHD and the components of biological motion processing have to remain speculative at this point because genetic influences were not explicitly tested in this paper.

We agree that the relationship between genetic factors and BM processing in ADHD needs more investigation, We have modified our statement in Discussion section as following:

“Using the classical twin method, Wang et al. found that the distinction between local and global BM processing may stem from the dissociated genetic bases. The former, to a great degree, seems to be acquired phylogenetically20,21,59,60, while the latter is primarily obtained through individual development19.” (lines 421 - 425),

Reviewer #2 (Public Review):

Summary:

Tian et al. aimed to assess differences in biological motion (BM) perception between children with and without ADHD, as well as relationships to indices of social functioning and possible predictors of BM perception (including demographics, reasoning ability and inattention). In their study, children with ADHD showed poorer performance relative to typically developing children in three tasks measuring local, global, and general BM perception. The authors further observed that across the whole sample, performance in all three BM tasks was negatively correlated with scores on the social responsiveness scale (SRS), whereas within groups a significant relationship to SRS scores was only observed in the ADHD group and for the local BM task. Local and global BM perception showed a dissociation in that global BM processing was predicted by age, while local BM perception was not. Finally, general (local & global combined) BM processing was predicted by age and global BM processing, while reasoning ability mediated the effect of inattention on BM processing.

Strengths:

Overall, the manuscript is presented in a relatively clear fashion and methods and materials are presented with sufficient detail so the study could be reproduced by independent researchers. The study uses an innovative, albeit not novel, paradigm to investigate two independent processes underlying BM perception. The results are novel and have the potential to have wide-reaching impact on multiple fields.

We appreciate your positive assessment of our work.

Weaknesses:

Except for the main analysis, it is unclear what the authors' specific predictions are regarding the three different tasks they employ. The three BM tasks are used to probe different processes underlying BM perception, but it is difficult to gather from the introduction why these three specific tasks were chosen and what predictions the authors have about the performance of the ADHD group in these tasks. Relatedly, the authors do not report whether (and if so, how) they corrected for multiple comparisons in their analyses. As the number of tests one should control for depends on the theoretical predictions (http://daniellakens.blogspot.com/2016/02/why-you-dont-need-to-adjust-you-alpha.html), both are necessary for the reader to assess the statistical validity of the results and any inferences drawn from them. The same is the case for the secondary analyses exploring relationships between the 3 individual BM tasks and social function measured by the social responsivity scale (SRS).

We appreciate these constructive suggestions. In response, we have included a detailed description in the Introduction section explaining why we employed three different tasks and our predictions about the performance in ADHD:

“Despite initial indications, a comprehensive investigation into BM perception in ADHD is warranted. We proposed that it is essential to deconstruct BM processing into its multiple components and motion features, since treating them as a single entity may lead to misleading or inconsistent findings31. To address this issue, we employed a carefully designed behavioral paradigm used in our previous study19, making slight adjustments to adapt for children. This paradigm comprises three tasks. Task 1 (BM-local) aimed to assess the ability to process local BM cues. Scrambled BM sequences were displayed and participants could use local BM cues to judge the facing direction of the scrambled walker. Task 2 (BM-global) tested the ability to process the global configuration cues of the BM walker. Local cues were uninformative, and participants used global BM cues to determine the presence of an intact walker. Task 3 (BM-general) tested the ability to process general BM cues (local + global cues). The stimulus sequences consisted of an intact walker and a mask containing similar target local cues, so participants could use general BM cues (local + global cues) to judge the facing direction of the walker.” (lines 116 - 130)

“In Experiment 1, we examined three specific BM perception abilities in children with ADHD. As mentioned earlier, children with ADHD also show impaired social interaction, which implies atypical social cognition. Therefore, we speculated that children with ADHD performed worse in the three tasks compared to TD children.” (lines 131 - 134)

Additionally, we have reported the p values corrected for multiple comparisons (false discovery rate, FDR) in the revised manuscript wherever it was necessary to adjust the alpha (lines 310 - 316; Table 2). The pattern of the results remained unchanged.

In relation to my prior point, the authors could provide more clarity on how the conclusions drawn from the results relate to their predictions. For example, it is unclear what specific conclusions the authors draw based on their findings that ADHD show performance differences in all three BM perception tasks, but only local BM is related to social function within this group. Here, the claim is made that their results support a specific hypothesis, but it is unclear to me what hypothesis they are actually referring to (see line 343 & following). This lack of clarity is aggravated by the fact that throughout the rest of the discussion, in particular when discussing other findings to support their own conclusions, the authors often make no distinction between the two processes of interest. Lastly, some of the authors' conclusions related to their findings on local vs global BM processing are not logically following from the evidence: For instance, the authors conclude that their data supports the idea that social atypicalities are likely to reduce with age in ADHD individuals. However, according to their own account, local BM perception - the only measure that was related to social function in their study - is understood to be age invariant (and was indeed not predicted by age in the present study).

Thank you for pointing out this issue. We have carefully revised the Discussion section about our findings to clarify these points:

“Our study contributes several promising findings concerning atypical biological motion perception in ADHD. Specifically, we observe the atypical local and global BM perception in children with ADHD. Notably, a potential dissociation between the processing of local and global BM information is identified. The ability to process local BM cues appears to be linked to the traits of social interaction among children with ADHD. In contrast, global BM processing exhibits an age-related development. Additionally, general BM perception may be affected by factors including attention.” (lines 387 - 393)

We have provided a detailed discussion on the two processes of interest to clarify their potential differences and the possible reasons behind the difference of the divergent developmental trajectories between local and global BM processing:

“BM perception is considered a multi-level phenomenon56-58. At least in part, processing information of local BM and global BM appears to involve different genetic and neural mechanisms16,19. Using the classical twin method, Wang et al. found that the distinction between local and global BM processing may stem from the dissociated genetic bases. The former, to a great degree, seems to be acquired phylogenetically20,21,59,60, while the latter is primarily obtained through individual development19. The sensitivity to local rather than global BM cues seems to emerge early in life. Visually inexperienced chicks exhibit a spontaneous preference for the BM stimuli of hen, even when the configuration was scrambled20. The same finding was reported in newborns. On the contrary, the ability to process global BM cues rather than local BM cues may be influenced by attention28,29 and shaped by experience24,56.” (lines 419 - 430)

“We found that the ability to process global and general BM cues improved significantly with age in both TD and ADHD groups, which imply the processing module for global BM cues tends to be mature with development. In the ADHD group, the improvement in processing general and global BM cues is greater than that in processing local BM cues, while no difference was found in TD group. This may be due to the relatively higher baseline abilities of BM perception in TD children, resulting in a relatively milder improvement. These findings also suggest a dissociation between the development of local and global BM processing. There seems to be an acquisition of ability to process global BM cues, akin to the potential age-related improvements observed in certain aspects of social cognition deficits among individuals with ADHD5, whereas local BM may be considered an intrinsic trait19.” (lines 438 -449)

In addition, we have rephased some inaccurate statements in revised manuscript. Another part of social dysfunction might be stable and due to the atypical local BM perception in ADHD individuals, although some studies found a part of social dysfunction would reduce with age in ADHD individuals. One reason is that some factors related to social dysfunction would improve with age, like the symptom of hyperactivity.

Results reported are incomplete, making it hard for the reader to comprehensively interpret the findings and assess whether the conclusions drawn are valid. Whenever the authors report negative results (p-values > 0.05), the relevant statistics are not reported, and the data not plotted. In addition, summary statistics (group means) are missing for the main analysis.

Thanks for your comments. We have provided the complete statistical results in the revised manuscript (lines 309 - 316) and supplementary material, which encompass relevant statistics and plots of negative results (Figure 4, Figure S2 and S3), in accordance with our research questions. And we have also included summary statistics in the Results section (lines 287 - 293).

Some of the conclusions/statements in the article are too strong and should be rephrased to indicate hypotheses and speculations rather than facts. For example, in lines 97-99 the authors state that the finding of poor BM performance in TD children in a prior study 'indicated inferior applicability' or 'inapplicable experimental design'. While this is one possibility, a perhaps more plausible interpretation could be that TD children show 'poor' performance due to outstanding maturation of the underlying (global) BM processes (as the authors suggest themselves that BM perception can improve with age). There are several other examples where statements are too strong or misleading, which need attention.

We thank you for pointing out the issue. We have toned down and rephrased the strong statements and made the necessary revisions.

“Another study found that children with ADHD performed worse in BM detection with moderate ratios of noise34. This may be due to the fact that BM stimuli with noise dots will increase the difficulty of identification, which highlights the difference in processing BM between the two groups33,35.” (lines 111 - 115)

Reviewer #3 (Public Review):

Summary:

The authors presented point light displays of human walkers to children (mean = 9 years) with and without ADHD to compare their biological motion perception abilities and relate them to IQ, social responsiveness scale (SRS) scores and age. They report that children with ADHD were worse at all three biological motion tasks, but that those loading more heavily on local processing related to social interaction skills and global processing to age. The important and solid findings are informative for understanding this complex condition, as well as biological motion processing mechanisms in general. However, I am unsure that these differences between local and global skills are truly supported by the data and suggest some further analyses.

Strengths:

The authors present clear differences between the ADHD and TD children in biological motion processing, and this question has not received as much attention as equivalent processing capabilities in autism. They use a task that appears well controlled. They raise some interesting mechanistic possibilities for differences in local and global motion processing, which are distinctions worth exploring. The group differences will therefore be of interest to those studying ADHD, as well as other developmental conditions, and those examining biological motion processing mechanisms in general.

We appreciate your positive feedback. In revised manuscript, we have added more analyses to support the differences between local and global motion processing. Please refer to our response to the point #3 you mentioned below.

Weaknesses:

I am unsure that the data are strong enough to support claims about differences between global and local processing wrt social communication skills and age. The mechanistic possibilities for why these abilities may dissociate in such a way are interesting, but do not seem so plausible to me. I am also concerned about gender, and possible autism, confounds when examining the effect of ADHD. Specifics:

Gender confound. There are proportionally more boys in the ADHD than TD group. The authors appear to attempt to overcome this issue by including gender as a covariate. I am unsure if this addresses the problem. The vast majority of participants in the ADHD group are male, and gender is categorically, not continuously, defined. I'm pretty sure this violates the assumptions of ANCOVA.

We appreciate your comments. We concur with you that although we observed a clear difference between local and global BM processing in ADHD, the evidence is to some extent preliminary. The mechanistic possibilities for why these abilities may dissociate have been discussed in revised manuscript. Please refer to the response to reviewer 2’s point #2. To further examine if gender played a role in the observed results, we used a statistical matching technique to obtain a sub-dataset. The pattern of results remained with the more balanced dataset (see Supplementary Information part 1). According to your suggestion, we have also presented the results without using gender as a covariate in main text and also separated the data of boys and girls on the plots (see Figure 1 and Figure S1). There were indeed no signs of a gender effect.

Autism. Autism and ADHD are highly comorbid. The authors state that the TD children did not have an autism or ADHD diagnosis, but they do not state that the ADHD children did not have an autism diagnosis. Given the nature of the claims, this seems crucial information for the reader.

Thanks for your suggestion. We have confirmed that all children with ADHD in our study were not diagnosed with autism. We used a semi-structured interview instrument (K-SADSPL-C) to confirm every recruited child with ADHD but not with ASD. The exclusion criteria for both groups were mentioned in the Materials and methods section:

“Exclusion criteria for both groups were: (a) neurological diseases; (b) other neurodevelopmental disorders (e.g., ASD, Mental retardation, and tic disorders), affective disorders and schizophrenia…” (lines 158 - 162)

Conclusions. The authors state frequently that it was the local BM task that related to social communication skills (SRS) and not the global tasks. However, the results section shows a correlation between SRS and all three tasks. The only difference is that when looking specifically within the ADHD group, the correlation is only significant for the local task. I think that if the authors wish to make strong claims here they must show inferential stats supporting (1) a difference between ADHD and TD SRS-Task 1 correlations, and (2) a difference in those differences for Task 2 and 3 relative to Task 1. I think they should also show a scatterplot of this correlation, with separate lines of best fit for the two groups, for Tasks 2 and 3 as well. I.e. Figure 4 should have 3 panels. I would recommend the same type of approach for age. Currently, they have small samples for correlations, and are reading much of theoretical significance between some correlations passing significance threshold and others not. It would be incredibly interesting if the social skills (as measured by SRS) only relate to local BM abilities, and age only to global, but I think the data are not so clear with the current information. I would be surprised if all BM abilities did not improve with age. Even if there is some genetic starter kit (and that this differs according to particular BM component), most abilities improve with learning/experience/age.

Thank you for this recommendation. We have added more statistics to test differences between the correlations (a difference between ADHD and TD in SRS-Task 1 correlations (see the first paragraph of Supplementary Information part 2), a difference in SRS-response accuracy correlations for Task 2 and 3 relative to Task 1(see the second paragraph of Supplementary Information part 2), and a difference in age-response accuracy correlations for Task 2 and 3 relative to Task 1 in ADHD group (see Supplementary Information part 3)). Additionally, we have included scatterplots for SRS-Task1, SRS-Task2, SRS-Task3 (with separate lines of best fit for the two groups in each, see Figure 4), SRS-ADHD, SRS-TD, age-ADHD and age-TD (with separate lines of best fit for the three tasks in each, see Figure S2 and S3) to make a clear demonstration. Detailed results have been presented in the revised manuscript and Supplementary Information. We expect these further analyses would strengthen our conclusions.

Theoretical assumptions. The authors make some sweeping statements about local vs global biological motion processing that need to be toned down. They assume that local processing is specifically genetically whereas global processing is a product of experience. The fact their global, but not local, task performance improves with age would tend to suggest there could be some difference here, but the existing literature does not allow for this certainty. The chick studies showing a neonatal preference are controversial and confounded - I cannot remember the specifics but I think there an upper vs lower visual field complexity difference here.

Thank you for pointing out this issue. We have toned down rephrased our claims that the difference between local and global BM processing according to your suggestion:

“These findings suggest that local and global mechanisms might play different roles in BM perception, though the exact mechanisms underlying the distinction remain unclear. Exploring the two components of BM perception will enhance our understanding of the difference between local and global BM processing, shedding light on the psychological processes involved in atypical BM perception.” (lines 87 - 92)

Reviewer #1 (Recommendations For The Authors):

I have only a number of minor points that should be addressed prior to publication:

L. 95ff: What is meant by 'inapplicability of experimental designs' ? This paragraph is somewhat unclear.

In revised manuscript, we have clarified this point (lines 111 - 115).

L. 146: The groups were not perfectly balanced for sex. Would results change fundamentally in a more balanced design, or can arguments be given that gender does not play a role, like it seems to be the case for some functions in biological motion perception (e.g. Pavlova et al. 2015; Tsang et al 2018). One could provide a justification that this disbalance does not matter or test for subsampled balanced data sets maybe.

This point is similar to the point #1 from reviewer 3, and we have addressed this issue in our response above.

L. 216 f.: In this paragraph it does not become very clear that the mask for the global task consisted of scrambles generated from walkers walking in the same direction. The mask for the local task then should consist of a balanced mask that contains the same amount of local motion cues indicating right and leftwards motion. Was this the case? (Not so clear from this paragraph.)

Regarding the local task, the introduction of mask would make the task too difficult for children. Therefore, in the local task, we only displayed a scrambled walker without a mask, which was more suitable for children to complete the task. We have made clear this point in the corresponding paragraph (lines 232 - 241).

L. 224 ff.: Here it would be helpful to see the 5 different 'facing' directions of the walkers. What does this exactly mean? Do they move on oblique paths that are not exactly orthogonal to the viewing directions, and how much did these facing directions differ?

Out of the five walkers we used, two faced straight left or right, orthogonal to the viewing directions. Two walked with their bodies oriented 45 degrees from the observer, to the left or right. The last one walked towards the observer. We have included a video (Video 4) to demonstrate the 5 facing directions.

L. 232: How was the number of 5 practicing trials determined/justified?

As mentioned in main text, global BM processing is susceptible to learning. Therefore, too many practicing trials would increase BM visual experience and influence the results. We determined the number of training trials to be 5 based on the results of the pilot experiment. During this phase, we observed that nearly all children were able to understand the task requirements well after completing 5 practicing trials.

L 239: Apparently no non-parametric statistics was applied. Maybe it would be good to mention in the Statistics section briefly why this was justified.

We appreciate your suggestion and have cited two references in the Statistics section (Fagerland et al. 2012, Rochon et al. 2012). Fagerland et al., mentioned that when the sample size increases, the t-test is more robust. According to the central limit theorem, when the sample size is greater than 30, the sampling distribution of the mean can be safely assumed to be normal.

(http://www2.psychology.uiowa.edu/faculty/mordkoff/GradStats/part%201/I.07%20normal.p df). In fact, we also ran non-parametric statistics for our data and found the results to be robust.

L 290: 'FIQ' this abbreviation should be defined.

Regarding the abbreviation ’FIQ’, it stands for the abbreviation of the full-scale intellectual quotient, which was mentioned in Materials and methods section:

“Scores of the four broad areas constitute the full-scale intellectual quotient (FIQ).”

L. 290 ff.: These model 'BM-local = age + gender etc ' is a pretty sloppy notation. I think what is meant that a GLM was used that uses the predictors gender etc. time appropriate beta_i values. This formula should be corrected or one just says that a GLM was run with the predictors gender ....

The same criticism applies to these other models that follow.

We thank you for pointing this out. We have modified all formulas accordingly in the revised manuscript (see part3 of the Results section).

All these models assume linearity of the combination of the predictors.was this assumption verified?

We referred to the previous study of BM perception in children. They found main predictor variables, including IQ (Rutherford et al., 2012; Jones et al., 2011) and age (Annaz et al., 2010; van et al., 2016), have a linear relation with the ability of BM processing.

L. 296ff.: For model (b) it looks like general BM performance is strongly driven by the predictor global BM performance in the group of patients. Does the same observation also apply to the normals?

The same phenomenon was not observed in TD children. We have briefly discussed this point in the Discussion section of the revised manuscript (lines 449 - 459).

Reviewer #2 (Recommendations For The Authors):

(1) Please add public access to the data repository so data availability can be assessed.

The data of the study will be available at https://osf.io/37p5s/.

(2) Although overall, the language was clear and understandable, there are a few parts where language might confuse a reader and lead to misconceptions. For instance, line 52: Did the authors mean to refer to 'emotions and intentions' instead of 'emotions and purposes'? See also examples where rephrasing may help to reflect a statement is speculation rather than fact.

Thanks for the comments. We have carefully checked the full text and rephrased the confused statements.

(3) Line 83/84: Autism is not a 'mental disorder' - please change to something like 'developmental disability'. Authors are encouraged to adapt their language according to terms preferred by the community (e.g., see Fig. 5 in this article:

https://onlinelibrary.wiley.com/doi/10.1002/aur.2864)

Suggestion well taken. We have changed the wording accordingly:

“In recent years, BM perception has received significant attention in studies of mental disorders (e.g., schizophrenia30) and developmental disabilities, particularly in ASD, characterized by deficits in social communication and social interaction31,32.” (lines 93 - 95)

(4) Please report how the sample size for the study was determined.

In the Materials and methods section (lines 168 - 173), we explained how the sample size was determined.

Line 94: It would be helpful to have a brief description of what neurophysiological differences have been observed upon BM perception in children with ADHD.

Thanks for the comment. We have added a brief description of neurophysiological findings in children with ADHD (lines 108 - 111).

(6) Line 106/107 and 108/109: please add references.

We have revised this part, and the relevant findings and references are in line with the revised manuscript (lines 77, 132 - 133).

(7) Line 292: Please add what order the factors were entered into each regression model.

Regarding this issue, we used SPSS 26 for the main analysis. SPSS utilizes the Type III sum of squares (default) to evaluate models. Regardless of the order in the GLM, we will obtain the same result. For more information, please refer to the documentation of SPSS 26 (https://www.ibm.com/docs/en/spss-statistics/26.0.0?topic=features-glm-univariate-analysis).

Reviewer #3 (Recommendations For The Authors)

(1) Task specifics. It is key to understanding the findings, as well as the dissociation between tasks, that the precise nature of the stimuli is clear. I think there is room for improvement in description here. Task 1 is described as involving relocating dots within the range of the intact walker. Of course, PLWs are created by presenting dots at the joints, so relocation can involve either moving to another place on the body, or random movement within the 2D spatial array (which likely involves moving it off the body). Which was done? It is said that Ps must indicate the motion direction, but what was the display of the walker? Sagittal? Task 2 requires detecting whether there is an intact walker amongst scrambled walkers. Were all walkers completely overlaid? Task 3 requires detecting the left v right facing of an intact walker at different orientations, presented amongst noise. So Task 3 requires determining facing direction and Task 1 walking direction. Are these tasks the same but described differently? Or can walkers ever walk backwards? Wrt this point, I also think it would help the reader if example videos were uploaded.

We appreciate you for bringing this to our attention. With regards to Task 1, it appears that your second speculation is correct. We scrambled the original dots and randomly presented them within the 2D spatial array (which likely involved moving them off the body). As a result, the global configuration of the 13 dots was completed disrupted while preserving the motion trajectory of each individual dot. This led to the display of scrambled dots on the monitor (which does not resemble a human). In practice, these local BM cues contain information about motion direction. In Task 2, the target walkers completely overlaid by a mask that is approximately 1.44 times the size of the intact walker. The task requirements of Task 1 and Task3 are same, which is judging the motion (walking) direction. The difference is that Task 1 displayed a scrambled walker while Task 3 displayed an intact walker within a mask. We have clarified these points and improved our descriptions in Procedure section and created example videos for each task, which we believe will be helpful for the readers to understand each task.

(2) Gender confound (see above). I think that the authors should present the results without gender as a covariate. Can they separate boys and girls on the plots with different coloured individual datapoints, such that readers can see whether it's actually a gender effect driving the supposed ADHD effect? And show that there are no signs of a gender effect in their TD group?

This point is similar to the point #1 you mentioned. Please refer to our response to that point above.

(3) Autism possible confound (see above). I think the authors must report whether any of the ADHD group had an autism diagnosis.

Please refer to the response for the point #2 your mentioned.

(4) Conclusions concerning differences between the local and global tasks wrt SRS and age (see above). I believe the authors should add stats demonstrating differences between the correlations to support such claims, as well as demonstrating appropriate scatterplots for SRS-Task 1, SRS-Task 2, SRS-Task 3 and age-Task 1, age-Task2 and age-Task 3 (with separate lines of best fit for the two groups in each).

Please refer to the response for the point #3 your mentioned.

(5) Theoretical assumptions (see above). I would suggest rephrasing all claims here to outline that these discussed mechanistic differences between local and global BM processing are only possibilities and not known on the basis of existing data.

Please refer to the response for the point #4 your mentioned.

eLife assessment

This manuscript represents a cleanly designed experiment for assessing biological motion processing in children (mean age = 9) with and without ADHD. The group differences concerning accuracy in global and local motion processing abilities are solid, but the analyses suggesting dissociable relationships between global and local processing and social skills, age, and IQ are inconclusive. The results are useful in terms of understanding ADHD and the ontogenesis of different components of the processing of biological motion.

Reviewer #1 (Public Review):

Summary:

The paper presents a nice study investigating the impairments of biological motion perception in individuals with ADHD in comparison with neurotypical controls. Motivated by the idea that there is a relationship between biological motion perception and social capabilities, the authors investigated the impairments of local and global (holistic) biological motion perception, the diagnosis status, and several additional behavioral variables that are affected in ADHS (IQ, social responsiveness, and attention / impulsivity). As well local as global biological motion perception is impaired in ADHD individuals. In addition, the study demonstrates a significant correlation between local biological motion perception skills and the social responsiveness score in the ADHD group, but not in controls. A path analysis in the ADHD group suggests that general performance in<br /> biological motion perception is influenced mainly by global biological motion perception performance and attentional and perceptual reasoning skills.

Strengths:

It is true that there exists not much work on biological motion perception and ADHD. Therefore, the presented study contributes an interesting new result to the biological motion literature, and adds potentially also new behavioral markers for this clinical group. The design of the study is straightforward and technically sound, and the drawn conclusions are supported by the presented results.

Weaknesses:

Some of the claims about the relationship between genetic factors and ADHD and the components of biological motion processing have to remain speculative at this point because genetic influences were not explicitly tested in this paper. Specifically, the hypothesis that the perception of human social interaction is critically based on a local mechanism for the detection of asymmetry in foot trajectories of walkers (this is what 'BL-local' really measures), or on the detection of live agents in cluttered scenes seems not very plausible.

Based on my last comments, now the discussion has been changed in a way that tries to justify the speculative claims by citing a lot of other speculative papers, which does not really address the problem. For example, the fact that chicks walk towards biological motion stimuli is interesting. To derive that this verifies a fundamental mechanism in human biological motion processing is extremely questionable, given that birds do not even have a cortex. Taking the argumentation of the authors serious, one would have to assume that the 'Local BM' mechanism is probably located in the mesencephalon in humans, and then would have to interact in some way with social perception differences of ADHD children. To me all this seems to make very strong (over-)claims. I suggest providing a much more modest interpretation of the interesting experimental result, based on what has been really experimentally shown by the authors and closely related other data, rather than providing lots of far-reaching speculations.

In the same direction, in my view, go claims like 'local BM is an intrinsic trait' (L. 448) , which is not only imprecise (maybe better 'mechanisms of processing of local BM cues') but also rather questionable. Likely, this' local processing of BM' is a lower level mechanisms, located probably in early and mid-levels of the visual cortex, with a possible influence of lower structures. It seems not really plausible that this is related to a classical trait variables in the sense of psychology, like personality, as seems to be suggested here. Also here I suggest a much more moderate and less speculative interpretation of the results.

Reviewer #2 (Public Review):

Summary:

Tian et al. aimed to assess differences in biological motion (BM) perception between children with and without ADHD, as well as relationships to indices of social functioning and possible predictors of BM perception (including demographics, reasoning ability and inattention). In their study, children with ADHD showed poorer performance relative to typically developing children in three tasks measuring local, global, and general BM perception. The authors further observed that across the whole sample, performance in all three BM tasks was negatively correlated with scores on the social responsiveness scale (SRS), whereas within groups a significant relationship to SRS scores was only observed in the ADHD group and for the local BM task. Local and global BM perception showed a dissociation in that global BM processing was predicted by age, while local BM perception was not. Finally, general (local & global combined) BM processing was predicted by age and global BM processing, while reasoning ability mediated the effect of inattention on BM processing.

Strengths:

Overall, the manuscript is presented in a clear fashion and methods and materials are presented with sufficient detail so the study could be reproduced by independent researchers. The study uses an innovative, albeit not novel, paradigm to investigate two independent processes underlying BM perception. The results are novel and have the potential to have wide-reaching impact on multiple fields.

Weaknesses:

The manuscript has greatly improved in clarity and methodological considerations in response to the review. There are only a few minor points which deserve the authors' attention:

When outlining the moviation for the current study, results from studies in ADHD and ASD are used too interchangeably. The authors use a lack of evidence for contributing (psychological/developmental) factors on BM processing in ASD to motivate the present study and refer to evidence for differences between typical and non-typical BM processing using studies in both ASD and ADHD. While there are certainly overlapping features between the two conditions/neurotypes, they are not to be considered identical and may have distinct etiologies, therefore the distinction between the two should be made clearer.

In the first/main analysis, is unclear to me why in the revised manuscript the authors changed the statistical method from ANOVA/ANCOVA to independent samples t-tests (unless the latter were only used for post-hoc comparisons, then this needs to be stated). Furthermore, although p-values look robust, for this analysis too it should be indicated whether and how multiple comparison problems were accounted for.

Reviewer #3 (Public Review):

Strengths:

The authors present differences between ADHD and TD children in biological motion processing, and this question has not received as much attention as equivalent processing capabilities in autism. They use a task that appears well controlled. They raise some interesting mechanistic possibilities for differences in local and global motion processing, which are distinctions worth exploring. The group differences will therefore be of interest to those studying ADHD, as well as other developmental conditions, and those examining biological motion processing mechanisms in general.

Weaknesses:

The data are not strong enough to support claims about differences between global and lobal processing wrt social communication skills and age. The mechanistic possibilities for why these abilities may dissociate in such a way are interesting, but the crucial tests of differences between correlations do not present a clear picture. Further empirical work would be needed to test the authors' claims. Specifics:

The authors state frequently that it was the local BM task that related to social communication skills (SRS) and not the global tasks. However, the results section shows a correlation between SRS and all three tasks. The only difference is that when looking specifically within the ADHD group, the correlation is only significant for the local task. The supplementary materials demonstrate that tests of differences between correlations present an incomplete picture. Currently they have small samples for correlations, so this is unsurprising.

Theoretical assumptions. The authors make some statements about local vs global biological motion processing that should still be made more tentatively. They assume that local processing is specifically genetically whereas global processing is a product of experience. These data in newborn chicks are controversial and confounded - I cannot remember the specifics but I think there an upper vs lower visual field complexity difference here.

Readability. The manuscript needs very careful proofreading and correction for grammar. There are grammatical errors throughout.

Author Response

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

General response:

We thank the reviewers for their thorough evaluation of our manuscript. Working on the raised concerns has improved the manuscript greatly. Specifically, the recommendations to clarify the adopted assumptions in the study strengthened the motivation for the study; further, following up some of the reviewers’ concerns with additional analyses validated our chosen measures and strengthened the compatibility of the findings with the predictions of the dynamic attending framework. Below, you will find our detailed point-by-point responses, along with information on specific revisions.

The reviewers pointed out that study assumptions were unclear, some of the measures we chose were not well motivated, and the findings were not well enough explained considering possible alternatives. As suggested, we reformulated the introduction, explained the common assumptions of entrainment models that we adopted in the study, and further clarified how our chosen measures for the properties of the internal oscillators relate to these assumptions.

We realized that the initial emphasis on the compatibility of the current findings with predictions of entrainment models might have led to the wrong impression that the current study aimed to test whether auditory rhythmic processing is governed by timekeeper or oscillatory mechanisms. However, testing these theoretical models to explain human behavior necessitates specific paradigms designed to compare the contrasting predictions of the models. A number of studies do so by manipulating regularity in a stimulus sequence or expectancy of stimulus onsets, or assessing the perceived timing of targets that follow a stimulus rhythm. Such paradigms allow testing the prediction that an oscillator, underlying perceptual timing, would entrain to a regular but not an irregular sequence. This would further lead to stronger expectancies at the peak of the oscillation, where 'attentional energy' is the highest. These studies report 'rhythmic facilitation', where targets that align with the peaks of the oscillation are better detected than those that do not (see Henry and Herrmann (2014) and Haegens and Zion Golumbic (2018) for reviews). Additionally, unexpected endings of standard intervals, preceded by a regular entraining sequence, lead to a biased estimation of subsequent comparison intervals, due to the contrast between the attentional oscillator's phase and a deviating stimulus onset (Barnes & Jones, 2000; Large & Jones, 1999; McAuley & Jones, 2003). Even a sequence rate that is the multiple of the to-be-judged standard and comparison intervals give rise to rhythmic facilitation (McAuley & Jones, 2003), and the expectancy of a stimulus onset modulates duration judgments. These findings are not compatible with predictions of timekeeper models as time intervals in these models are represented arbitrarily and are not affected by expectancy violations.

In the current study, we adopted an entrainment approach to timing, rather than testing predictions of competing models. This choice was motivated by several aspects of entrainment models that align better with the aims of the current study. First, our focus was on understanding perception and production of rhythms, for which perception is better explained by entrainment models than by timekeeper models, which excel at explaining perception of isolated time intervals (McAuley, 2010). Moreover, we wanted to leverage the fact that entrainment models elegantly include parameters that can explain different aspects of timing abilities, and these parameters can be estimated in an individualized manner. For instance, the flexibility property of oscillators can be linked to the ability to adapt to changes in external context, while timekeeper or Bayesian timing approaches lack a specific mechanism to quantify temporal adaptation across perceptual and motor domains. Finally, that entrainment is observed across theoretical, behavioral, and neural levels renders entrainment models useful in explaining and generalizing behavior across different domains. Nevertheless, some results showed partial compatibility with predictions of the timekeeper models, such as the modulation of 'bestperformance rates' by the temporal context, observed in Experiment 1’ random-order sessions, where stimulus rates maximally differed across consecutive trials. However, given that the mean, standard deviation, and range of stimulus rates were identical across sessions, and timekeeper models assume no temporal adaptation in duration perception, we should have observed similar results across these sessions. Conversely, we found significant accuracy differences, biased duration judgments, and harmonic relationships between the best-performance rates. We elaborate more on these results with respect to their compatibility with the contrasting models of human temporal perception in the revised discussion.

Responses to specific comments:

(1.1) At times, I found it challenging to evaluate the scientific merit of this study from what was provided in the introduction and methods. It is not clear what the experiment assumes, what it evaluates, and which competing accounts or predictions are at play. While some of these questions are answered, clear ordering and argumentative flow is lacking. With that said, I found the Abstract and General Discussion much clearer, and I would recommend reformulating the early part of the manuscript based on the structure of those segments.

Second, in my reading, it is not clear to what extent the study assumes versus demonstrates the entrainment of internal oscillators. I find the writing somewhat ambiguous on this count: on the one hand, an entrainment approach is assumed a priori to design the experiment ("an entrainment approach is adopted") yet a primary result of the study is that entrainment is how we perceive and produce rhythms ("Overall, the findings support the hypothesis that an oscillatory system with a stable preferred rate underlies perception and production of rhythm..."). While one could design an experiment assuming X and find evidence for X, this requires testing competing accounts with competing hypotheses -- and this was not done.

We appreciate the reviewer’s concerns and suggestion to clarify the assumptions of the study and how the current findings relate to the predictions of competing accounts. To address these concerns:

• We added the assumptions of the entrainment models that we adopted in the Introduction section and reformulated the motivation to choose them accordingly.

• We clarified in the Introduction that the study’s aim was not to test the entrainment models against alternative theories of rhythm perception.

• We added a paragraph in the General Discussion to further distinguish predictions from the competing accounts. Here we discussed the compatibility of the findings with predictions of both entrainment and timekeeper models.

• We rephrased reasoning in the Abstract, Introduction, and General Discussion to further clarify the aims of the study, and how the findings support the hypotheses of the current study versus those of the dynamic attending theory.

(1.2) In my view, more evidence is required to bolster the findings as entrainment-based regardless of whether that is an assumption or a result. Indeed, while the effect of previous trials into the behaviour of the current trial is compatible with entrainment hypotheses, it may well be compatible with competing accounts as well. And that would call into question the interpretation of results as uncovering the properties of oscillating systems and age-related differences in such systems. Thus, I believe more evidence is needed to bolster the entrainment hypothesis.

For example, a key prediction of the entrainment model -- which assumes internal oscillators as the mechanism of action -- is that behaviour in the SMT and PTT tasks follows the principles of Arnold's Tongue. Specifically, tapping and listening performance should worsen systematically as a function of the distance between the presented and preferred rate. On a participant-by-participant, does performance scale monotonically with the distance between the presented and preferred rate? Some of the analyses hint at this question, such as the effect of 𝚫IOI on accuracy, but a recontextualization, further analyses, or additional visualizations would be helpful to demonstrate evidence of a tongue-like pattern in the behavioural data. Presumably, non-oscillating models do not follow a tongue-like pattern, but again, it would be very instructive to explicitly discuss that.

We thank the reviewer for the excellent suggestion of assessing 'Arnold's tongue' principles in timing performance. We agree that testing whether timing performance forms a pattern compatible with an Arnold tongue would further support our assumption that the findings related to preferred rate stem from an entrainment-based mechanism. We rather refer to the ‘entrainment region’, (McAuley et al., 2006) that corresponds to a slice in the Arnold tongue at a fixed stimulus intensity that entrains the internal oscillator. In both representations of oscillator behavior across a range of stimulus rates, performance should systematically increase as the difference between the stimulus rate and the oscillator's preferred rate, namely, 'detuning' decreases. In response to the reviewer’s comment, we ran further analyses to test this key prediction of entrainment models. We assessed performance at stimulus rates that were faster and slower than an individual's preferred rate estimates from in Experiment 1. To do so, we ran logistic regression models on aggregated datasets from all participants and sessions, where normalized IOI, in trials where the stimulus rate was faster than the preferred rate estimate, and in those where it was slower, predicted accuracy. Stimulus IOIs were normalized within each direction (faster- versus slower-than-preferred rate) using z-score transformation, and the direction was coded as categorical in the model. We reasoned that a positive slope for conditions with stimulus rates faster than IOI, and a negative slope from conditions with slower rates, should indicate a systematic accuracy increase toward the preferred rate estimate. This is exactly what we found. These results revealed significant main effect for the IOI and a significant interaction between IOI and direction, indicating that accuracy increased towards the preferred rate at fast rates and decreased as the stimulus rate diverged from the preferred rate at slow rates. We added these results to the respective subsections of Experiment 1 Methods and Results, added a plot showing the slices of the regression surfaces to Figure 2B and elaborated on the results in Experiment 1 Discussion. As the number of trials in Experiment 2 was much lower (N = 81), we only ran these additional analyses in Experiment 1.

(1.3) Fourth, harmonic structure in behaviour across tasks is a creative and useful metric for bolstering the entrainment hypothesis specifically because internal oscillators should display a preference across their own harmonics. However, I have some doubts that the analyses as currently implemented indicate such a relationship. Specifically, the main analysis to this end involves summing the residuals of the data closest to y=x, y=2*x and y=x/2 lines and evaluating whether this sum is significantly lower than for shuffled data. Out of these three dimensions, y=x does not comprise a harmonic, and this is an issue because it could by itself drive the difference of summed residuals with the shuffled data. I am uncertain whether rerunning the same analysis with the x=y dimension excluded constitutes a simple resolution because presumably there are baseline differences in the empirical and shuffled data that do not have to do with harmonics that would leak into the analysis. To address this, a simulation with ground truths could be helpful to justify analyses, or a different analysis that evaluates harmonic structure could be thought of.

We thank the reviewer for pointing out the weakness of the permutation test we developed to assess the harmonic relationship between Experiment 1’s preferred rate estimates. Datapoints that fall on the y=x line indeed do not represent harmonic relationships. They rather indicate one-to-one correspondence between the axes, which is a stronger indicator of compatibility between the estimates. Maybe speaking to the reviewer’s point, standard correlation analyses were not significant, which would have been expected if the permutation results were being driven by the y=x relationship. This was the reason we developed the permutation test to include integer-ratio datapoints could also contribute.

Based on reviewer’s comment, we ran additional analyses to assess the harmonic relationships between the estimates. The first analysis involved a circular approach. We first normalized each participant’s estimates by rescaling the slower estimate with respect to the faster one by division; and converted the values to radians, since a pair of values with an integer-ratio relationship should correspond to the same phase on a unit circle. Then, we assessed whether the resulting distribution of normalized values differed from a uniform distribution, using Rayleigh’s test, which was significant (p = .004). The circular mean of the distribution was 44 (SD = 53) degrees (M = 0.764, SD = 0.932 radians), indicating that the slower estimates were slightly slower than the fast estimate or its duplicates. As this distribution was skewed toward positive values due to the normalization procedure, we did not compare it against zero angle. Instead, we ran a second test, which was a modular approach. We first calculated how much the slower estimate deviated proportionally from the faster estimate or its multiples (i.e., subharmonics) by normalizing the estimates from both sessions by the faster estimate. The outcome measure was the modulus of the slower, relative to the faster estimate, divided by the faster estimate. Then, we ran a permutation test, shuffling the linear-order session estimates over 1000 iterations and taking the median percent deviation values for each iteration. The test statistic was significant (p = .004), indicating that the harmonic relationships we observed in the estimates were not due to chance or dependent on the assessment method. We added these details of additional analyses to assess harmonic relationships between the Experiment 1 preferred rate estimates in the Supplementary Information.

(2.1) The current study is presented in the framework of the ongoing debate of oscillator vs. timekeeper mechanisms underlying perceptual and motor timing, and authors claim that the observed results support the former mechanism. In this line, every obtained result is related by the authors to a specific ambiguous (i.e., not clearly related to a biophysical parameter) feature of an internal oscillator. As pointed out by an essay on the topic (Doelling & Assaneo, 2021), claiming that a pattern of results is compatible with an "oscillator" could be misleading, since some features typically used to validate or refute such mechanisms are not well grounded on real biophysical models. Relatedly, a recent study (Doelling et al., 2022) shows that two quantitatively different computational algorithms (i.e., absolute vs relative timing) can be explained by the same biophysical model. This demonstrates that what could be interpreted as a timekeeper, or an oscillator can represent the same biophysical model working under different conditions. For this reason, if authors would like to argue for a given mechanism underlying their observations, they should include a specific biophysical model, and test its predictions against the observed behavior. For example, it's not clear why authors interpret the observation of the trial's response being modulated by the rate of the previous one, as an oscillator-like mechanism underlying behavior. As shown in (Doelling & Assaneo, 2021) a simple oscillator returns to its natural frequency as soon as the stimulus disappears, which will not predict the long-lasting effect of the previous trial. Furthermore, a timekeeper-like mechanism with a long enough integration window is compatible with this observation.

Still, authors can choose to disregard this suggestion, and not testing a specific model, but if so, they should restrict this paper to a descriptive study of the timing phenomena.

We thank the reviewer for their valuable suggestion of to include a biophysical model to further demonstrate the compatibility of the current findings with certain predictions of the model. While we acknowledge the potential benefits of implementing a biophysical model to understand the relationships between model parameters and observed behavior, this goes beyond the scope of the current study.

We note that we have employed a modeling approach in a subsequent study to further explore how the properties and the resulting behavior of an oscillator map onto the patterns of human behavior we observed in the current study (Kaya & Henry, 2024, February 5). In that study, we fitted a canonical oscillator model, and several variants thereof, separately to datasets obtained from random-order and linear-order sessions of Experiment 1 of the current submission. The base model, adapted from McAuley and Jones (2003), assumed sustained oscillations within the trials of the experiment, and complete decay towards the preferred rate between the trials. We introduced a gradual decay parameter (Author response image 1A) that weighted between the oscillator's concurrent period value at the time of decay and its initial period (i.e., preferred rate). This parameter was implemented only within trials, between the standard stimulus sequence and comparison interval in Variant 1, between consecutive trials in Variant 2, and at both temporal locations in Variant 3. Model comparisons (Author response image 1B) showed that Variant 3 was the best-fitting model for both random- and linear-order datasets. Crucially, estimates for within- and between-trial decay parameters, obtained from Variant 3, were positively correlated, suggesting that oscillators gradually decayed towards their preferred rate at similar timescales after cessation of a stimulus.

Author response image 1.

(A) Illustration of the model fitted to Experiment 1 datasets and (B) model comparison results. In each trial, the model is initialized with a phase (ɸ) and period (P) value. A At the offset of each stimulus interval i, the model updates its phase (pink arrows) and period (blue arrows) depending on the temporal contrast (C) between the model state and stimulus onset and phase and period correction weights, Wɸ and Wp. Wdecaywithin updates the model period as a weighted average between the period calculated for the 5th interval, P5, and model’s preferred rate, P0. C, calculated at the offset of the comparison interval. Wdecaybetween parameter initializes the model period at the beginning of a new trial as a weighted average between the last period from the previous trial and P0. The base model’s assumptions are marked by asterisks, namely sustained oscillation during the silence (i=5), and complete decay between trials. B Left: The normalized probability of each model having the minimum BIC value across all models and across participants. Right: AICc, calculated from each model’s fit to participants’ single-session datasets. In both panels, random-order and linear-order sessions were marked in green and blue, respectively. B denotes the base model, and V1, V2 and V3 denote variants 1, 2 and 3, respectively.

Although our behavioral results and modeling thereof must necessarily be interpreted as reflecting the mechanics of an attentional, but not a neural oscillator, these findings might shed light on the controversy in neuroscience research regarding the timeline of entrainment decay. While multiple studies show that neural oscillations can continue at the entrained rate for a number of cycles following entrainment (Bouwer et al., 2023; Helfrich et al., 2017; Lakatos et al., 2013; van Bree et al., 2021), different modeling approaches reveal mixed results on this phenomenon. Whereas Doelling and Assaneo (2021) show that a Stuart-Landau oscillator returns immediately back to its preferred rate after synchronizing to an external stimulus, simulations of other oscillator types suggest gradual decay toward the preferred rate (Large, 1994; McAuley, 1995; Obleser et al., 2017) or self-sustained oscillation at the external stimulus rate (Nachstedt et al., 2017).

While the Doelling & Assaneo study (2021) provides insights on entrainment and behavior of the Stuart-Landau oscillator under certain conditions, the internal oscillators hypothesized by the dynamic attending theory might have different forms, therefore may not adhere to the behavior of a specific implementation of an oscillator model. Moreover, that a phase-coupled oscillator does not show gradual decay does not preclude that models with period tracking behave similarly. Adaptive frequency oscillators, for instance, are able to sustain the oscillation after the stimulus ceases (Nachstedt et al., 2017). Alongside with models that use Hebbian learning (Roman et al., 2023), the main implementations of the dynamic attending theory have parameters for period tracking and decay towards the preferred rate (Large, 1994; McAuley, 1995). In fact, the u-shaped pattern of duration discrimination sensitivity across a range of stimulus rates (Drake & Botte, 1993) is better explained by a decaying than a non-decaying oscillator (McAuley, 1995). To conclude, the literature suggests that the emergence of decay versus sustain behavior of the oscillators and the timeline of decay depend on the particular model used as well as its parameters and does therefore not offer a one-for-all solution.

Reviewer #2 (Recommendations For The Authors):

• Are the range, SD and mean of the random-order and linear-order sessions different? If so, why?

Information regarding the SD and mean of the random-order and linear-order sessions was added to Experiment 1 Methods section.

“While the mean (M = 599 ms), standard deviation (SD = 231 ms) and range (200, 998 ms) of the presented stimulus IOIs were identical between the sessions, the way IOI changed from trial to trial was different.“ (p. 5)

• Perhaps the title could mention the age-related flexibility effect you demonstrate, which is an important contribution that without inclusion in the title could be missed in literature searches.

We have changed the title to include age-related changes in oscillator flexibility. Thanks for the great suggestion.

• Is the statistical analysis in Figure 4A between subjects? Shouldn't the analyses be within subjects?

We have now better specified that the statistical analyses of Experiment 2’s preferred rate estimates were across the tasks, in Figure 4 caption.

"Vertical lines above the box plots represent within-participants pairwise comparisons." (p. 17)

• It says participants' hearing thresholds were measured using standard puretone audiometry. What threshold warranted participant exclusion and how many participants were excluded on the basis of hearing skills?

We have now clarified that hearing threshold was not an exclusion criterion.

"Participants were not excluded based on hearing threshold." (p. 11)

• "Tapping rates from 'fastest' and 'slowest' FMT trials showed no difference between pre- and postsession measurements, and were additionally correlated across repeated measurements" - could you point to the statistics for this comparison?

Table 2 includes the results from both experiments’ analyses on unpaced tapping. (p. 10)

“The results of the pairwise comparisons between tapping rates from all unpaced tapping tasks across measurements are provided in Table 2.” (p. 15)

• How was the loudness (dB) of the woodblock stimuli determined on a participant-by-participant basis? Please ignore if I missed this.

Participants were allowed to set the volume to a comfortable level.

"Participants then set the sound volume to a level that they found comfortable for completing the task." (p. 4)

• Please spell out IOI, DEV, and other terms in full the first time they are mentioned in the manuscript.

We added the descriptions of abbreviations before their initial mention.

"In each experimental session, 400 unique trials of this task were presented, each consisting of a combination of the three main independent variables: the inter-onset interval, IOI; amount of deviation of the comparison interval from the standard, DEV, and the amount of change in stimulus IOI between consecutive trials, 𝚫IOI. We explain each of these variables in detail in the next paragraphs." (p. 4)

• Small point: In Fig 1 sub-text, random order and linear order are explained in reverse order from how they are presented in the figure.

We fixed the incompatibility between of Figure 1 content and caption.

• Small point: I found the elaborate technical explanation of windowing methods, including alternatives that were not used, unnecessary.

We moved the details of the smoothing analysis to the Supplementary Information.

• With regard to the smoothing explanation, what is an "element"? Is this a sample? If so, what was the sampling rate?

We reworded ‘element’ as ‘sample’. In the smoothing analyses, the sampling rate was the size of the convolution window, which was set to 26 for random-order, 48 for linear-order sessions.

• Spelling/language error: "The pared-down", "close each other", "always small (+4 ms), than".

We fixed the spelling errors.

Reviewer #3 (Recommendations For The Authors):

• My main concern is the one detailed as a weakness in the public review. In that direction, if authors decide to keep the mechanistic interpretation of the outcomes (which I believe is a valuable one) here I suggest a couple of models that they can try to adapt to explain the pattern of results:

a. Roman, Iran R., et al. "Hebbian learning with elasticity explains how the spontaneous motor tempo affects music performance synchronization." PLOS Computational Biology 19.6 (2023): e1011154.

b. Bose, Amitabha, Áine Byrne, and John Rinzel. "A neuromechanistic model for rhythmic beat generation." PLoS Computational Biology 15.5 (2019): e1006450.

c. Egger, Seth W., Nhat M. Le, and Mehrdad Jazayeri. "A neural circuit model for human sensorimotor timing." Nature Communications 11.1 (2020): 3933.

d. Doelling, K. B., Arnal, L. H., & Assaneo, M. F. (2022). Adaptive oscillators provide a hard-coded Bayesian mechanism for rhythmic inference. bioRxiv, 2022-06

Thanks for the suggestion! Please refer to our response (2.1.) above. To summarize, although we considered a full, well-fleshed-out modeling approach to be beyond the scope of the current work, we are excited about and actively working on exactly this. Our modeling take is available as a preprint (Kaya & Henry, 2024, February 5).

• Since the authors were concerned with the preferred rate they circumscribed the analysis to extract the IOI with better performance. Would it be plausible to explore how is the functional form between accuracy and IOI? This could shed some light on the underlying mechanism.

Unfortunately, we were unsure about what the reviewer meant by the functional form between accuracy and IOI. We interpret it to mean a function that takes IOI as input and outputs an accuracy value. In that case, while we agree that estimating this function might indeed shed light on the underlying mechanisms, this type of analysis is beyond the scope of the current study. Instead, we refer the reviewer and reader to our modeling study (please see our response (2.1.) above) that includes a model which takes the stimulus conditions, including IOI, and model parameters for preferred rate, phase and period correction and within- and between-trial decay and outputs predicted accuracy for each trial. We believe that such modeling approach, as compared to a simple function, gives more insights regarding the relationship between oscillator properties and duration perception.

• Is the effect caused by the dIOI modulated by the distance to the preferred frequency?

We thank the reviewer for the recommendation. We measured flexibility by the oscillator's ability to adapt to on-line changes in the temporal context (i.e., effect of 𝚫IOI on accuracy), rather than by quantifying the range of rates with improved accuracy. Nevertheless, we acknowledge that distance to the preferred rate should decrease accuracy, as this is a key prediction of entrainment models. In fact, testing this prediction was recommended also by the other reviewer, in response to which we ran additional analyses. These analyses involved assessment of the relationship between accuracy and detuning. Specifically, we assessed accuracy at stimulus rates that were faster and slower than an individual's preferred rate estimates from in Experiment 1. We ran logistic regression models on aggregated datasets from all participants and sessions, where accuracy was predicted by z-scored IOI, from trials where the stimulus rate was faster than the preferred rate estimate, and in those where it was slower. The model had a significant main effect of IOI and an interaction between IOI and direction (i.e., whether stimulus rate was faster or slower than the preferred rate estimate), indicating that accuracy increased towards the preferred rate at fast rates and decreased as the stimulus rate diverged from the preferred rate at slow rates. We added information regarding this analysis to the respective subsections of Experiment 1 Methods and Results, added a plot showing the slices of the regression surfaces to Figure 2B and elaborated on the results in Experiment 1 Discussion. As the number of trials in Experiment 2 was insufficient, we only ran these additional analyses in Experiment 1. We agree that a range-based measure of oscillator flexibility would also index the oscillators’ adaptive abilities. However, the current paradigms were designed for assessment of temporal adaptation. Thus, comparison of the two approaches to measuring oscillator flexibility, which can be addressed in future studies, is beyond the scope of the current study.

• Did the authors explore if the "motor component" (the difference between the motor and perceptual rates) is modulated by the participants age?

In response to the reviewer’s comment, we correlated the difference between the motor and perceptual rates with age, which was nonsignificant.

• Please describe better the slider and the keypress tasks. For example, what are the instructions given to the participant on each task, and how they differ from each other?

We added the Experiment 2 instructions in Appendix A.

• Typos: The caption in figure one reads 2 ms, while I believe it should say 200. Page 4 mentions that there are 400 trials and page 5 says 407.

We fixed the typos.

References

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eLife assessment

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

Reviewer #1 (Public Review):

Summary:

This study assumes but also demonstrates that auditory rhythm processing is produced by internal oscillating systems and evaluates the properties of internal oscillators across individuals. The authors designed an experiment and performed analyses that address individuals' preferred rate and flexibility, with a special focus on how much past rhythms influence subsequent trials. They find evidence for such historical dependence and show that we adapt less well to new rhythms as we age. While I have some doubts about the entrainment-based interpretation of the results, this work offers a useful contribution to our understanding of individual differences in rhythm processing regardless.

Strengths:

The inclusion of two tasks -- a tapping and a listening task -- complement each other methodologically. By analysing both the production and tracking of rhythms, the authors emphasize the importance of the characteristics of the receiver, the external world, and their interplay. The relationship between the two tasks and components within tasks are explored using a range of analyses. The visual presentation of the results is very clear. The age-related changes in flexibility are useful and compelling.

The paper includes a discussion of the study assumptions, and it contextualizes itself more explicitly as taking entrainment frameworks as a starting point. As such, even if the entrainment of oscillators cannot be decisively shown, it is now clear that this is nevertheless adopted as a useful theoretical lens.

Weaknesses:

The newly included analyses that justify an entrainment or oscillator-based interpretation of the result could be presented in a clearer manner so that readers can parse their validity better. For example, in line with an entrainment interpretation, the regression lines in Figure 2B show accuracy increases as the IOI moves towards the preferred rate -- but then beyond the preferred rate, accuracy appears to increase further still. Furthermore, the additional analyses on harmonic relationships could be enriched with justification and explanation of each of its steps.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

Author Response

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

Reviewer #1 (Recommendations For The Authors):

I only have a few minor suggestions:

Abstract: I really liked the conclusion (that IM and VWM are two temporal extremes of the same process) as articulated in lines 557--563. (It is always satisfying when the distinction between two things that seem fundamentally different vanishes). If something like this but shorter could be included in the Abstract, it would highlight the novel aspects of the results a little more, I think.

Thank you for this comment. We have added the following to the abstract:

“A key conclusion is that differences in capacity classically thought to distinguish IM and VWM are in fact contingent upon a single resource-limited WM store.”

L 216: There's an orphan parenthesis in "(justifying the use".

Fixed.

L 273: "One surprising result was the observed set size effect in the 0 ms delay condition". In this paragraph, it might be a good idea to remind the reader of the difference between the simultaneous and zero-delay conditions. If I got it right, the results differ between these conditions because it takes some amount of processing time to interpret the cue and free the resources associated with the irrelevant stimuli. Recalling that fact would make this paragraph easier to digest.

That is correct. However, at this point in the text, we have not yet fitted the DyNR model to the data. Therefore, we believe that introducing cue processing and resource reallocation as concepts that differentiate between those two conditions would disrupt the flow of this paragraph. We address these points soon after, in a paragraph starting on line 341.

Figures 3, 5: The labels at the bottom of each column in A would be more clear if placed at the top of each column instead. That way, the x-axis for the plots in A could be labeled appropriately, as "Error in orientation estimate" or something to that effect.

We edited both figures, now Figure 4 and Figure 6, as suggested.

L 379: It should be "(see Eq 6)", I believe.

That is correct, line 379 (currently line 391) should read ‘Eq 6’. Fixed.

L 379--385: I was a bit mystified as to why the scaled diffusion rate produced a worse fit than a constant rate. I imagine the scaled version was set to something like

sigma^2_diff_scaled = sigma^2_base + K*(N-1)

where N is the set size and sigma^2_base and K are parameters. If this model produced a similar fit as with a constant diffusion rate, the AIC would penalize it because of the extra parameter. But why would the fit be worse (i.e., not match the pattern of variability)? Shouldn't the fitter just find that the K=0 solution is the best? Not a big deal; the Nelder-Mead solutions can wobble when that many parameters are involved, but if there's a simple explanation it might be worth commenting on.

The scaled diffusion was implemented by extending Eq 6 in the following way:

σ(t)2 = (t-toffset) * σ̇ 2diff * N

where N is set size. Therefore, the scaling was not associated with a free parameter that could become 0 if set size did not affect diffusion rate, but variability rather mandatory increased with set size. We now clarify this in the text:

“The second variant was identical to the proposed model, except that we replaced the constant diffusion rate with a set size scaled diffusion rate by multiplying the right side of Eq 6 by N.“

Figure 4 is not mentioned in the main text. Maybe the end of L 398 would be a good place to point to it. The paragraph at L 443-455 would also benefit from a couple of references to it.

Thank you for this suggestion. Figure 4 (now Figure 5) was previously mentioned on line 449 (previously line 437), but now we have included it on line 410 (previously line 398), within the paragraph spanning lines 455-467 (previously 443-455), and also on line 136 where we first discuss masking effects.

L 500: Figure S7 is mentioned before Figures S5 and S6. Quite trivial, I know....

Thank you for this comment. There was no specific reason for Figure S7 to appear after S5 & S6, so we simply swapped their order to be consistent with how they are referred to in the manuscript (i.e., S7 became S5, S5 became S6, and S6 became S7).

Reviewer #2 (Recommendations For The Authors):

(1) One potential weakness is that the model assumes sensory information is veridical. However, this isn't likely the case. Acknowledging noise in sensory representations could affect the model interpretation in a couple of different ways. First, neurophysiological recordings have shown normalization affects sensory representations, even when a stimulus is still present on the screen. The DyNR model partially addresses this concern because reports are drawn from working memory, which is normalized. However, if sensory representations were also normalized, then it may improve the model variant where subjects draw directly from sensory representations (an alternative model that is currently described but discarded).

Thank you for this suggestion. We can consider two potential mechanisms through which divisive normalization might be incorporated into sensory processing within the DyNR model.

The first possibility involves assuming that normalization is pre-attentive. In this scenario, the sensory activity of each object would be rescaled at the lowest level of sensory processing, occurring before the allocation of attentional or VWM resources. One strong prediction of such an implementation is that recall error in the simultaneous cue condition (Experiment 1) should vary with set size. However, this prediction is inconsistent with the observed data, which failed to show a significant difference between set sizes, and is more closely aligned with the hypothesis of no-difference (F(2,18) = 1.26, p = .3, η2 = .04, BF10 = 0.47). On that basis, we anticipate that introducing normalization as a pre-attentive mechanism would impair the model fit.

An alternative scenario is to consider normalization as post-attentive. In the simultaneous cueing condition, only one item is attended (i.e., the cued one), regardless of the displayed set size. Here, we would expect normalized activity for a single item, regardless of the number of presented objects, which would then be integrated into VWM. This expanded DyNR model with post-attentive normalization would make exactly the same predictions as the proposed DyNR for recall fidelity, so distinguishing between these models would not be possible based on working memory experiments.

To acknowledge the possibility that sensory signals could undergo divisive normalization and to motivate future research, we have added the following to our manuscript:

“As well as being implicated in higher cognitive processes including VWM (Buschman et al, 2011; Sprague et al., 2014), divisive normalization has been shown to be widespread in basic sensory processing (Bonin et al., 2005; Busse et al., 2009; Ni et al., 2017). The DyNR model presently incorporates the former but not the latter type of normalization. While the data observed in our experiments do not provide evidence for normalization of sensory signals (note comparable recall errors across set size in the simultaneous cue condition of Experiment 1), this may be because sensory suppressive effects are localized and our stimuli were relatively widely separated in the visual field: future research could explore the consequences of sensory normalization for recall from VWM using, e.g., centre-surround stimuli (Bloem et al., 2018).”

Bloem, I. M., Watanabe, Y. L., Kibbe, M. M., & Ling, S. (2018). Visual Memories Bypass Normalization. Psychological Science, 29(5), 845–856. https://doi.org/10.1177/0956797617747091

Bonin, V., Mante, V., & Carandini, M. (2005). The Suppressive Field of Neurons in Lateral Geniculate Nucleus. The Journal of Neuroscience, 25(47), 10844–10856. https://doi.org/10.1523/JNEUROSCI.3562-05.2005

Buschman, T. J., Siegel, M., Roy, J. E., & Miller, E. K. (2011). Neural substrates of cognitive capacity limitations. Proceedings of the National Academy of Sciences, 108(27), 11252–11255. https://doi.org/10.1073/pnas.1104666108

Busse, L., Wade, A. R., & Carandini, M. (2009). Representation of Concurrent Stimuli by Population Activity in Visual Cortex. Neuron, 64(6), 931–942. https://doi.org/10.1016/j.neuron.2009.11.004

Ni, A. M., & Maunsell, J. H. R. (2017). Spatially tuned normalization explains attention modulation variance within neurons. Journal of Neurophysiology, 118(3), 1903–1913. https://doi.org/10.1152/jn.00218.2017

Sprague, T. C., Ester, E. F., & Serences, J. T. (2014). Reconstructions of Information in Visual Spatial Working Memory Degrade with Memory Load. Current Biology, 24(18), 2174–2180. https://doi.org/10.1016/j.cub.2014.07.066

Second, visual adaptation predicts sensory information should decrease over time. This would predict that for long stimulus presentation times, the error would increase. Indeed, this seems to be reflected in Figure 5B. This effect is not captured by the DyNR model.

Indeed, neural responses in the visual cortex have been observed to quickly adapt during stimulus presentation, showing reduced responses to prolonged stimuli after an initial transient (Groen et al., 2022; Sawamura et al., 2006; Zhou et al., 2019). This adaptation typically manifests as 1) reduced activity towards the end of stimulus presentation and 2) a faster decay towards baseline activity after stimulus offset.

In the DyNR model, we use an idealized solution in which we convolve the presented visual signal with a response function (i.e., temporal filter). At the longest presentation durations, in DyNR, the sensory signal plateaus and remains stable until stimulus offset. Because our psychophysical data does not allow us to identify the exact neural coding scheme that underlies the sensory signal, we tend to favour this simple implementation, which is broadly consistent with some previous attempts to model temporal dynamics in sensory responses (e.g., Carandini and Heeger, 1994). However, we agree with the reviewer that some adaptation of the sensory signal with prolonged presentation would also be consistent with our data.

We have added the following to the manuscript:

“In Experiment 2, the longest presentation duration shows an upward trend in error at set sizes 4 and 10. While this falls within the range of measurement error, it is also possible that this is a meaningful pattern arising from visual adaptation of the sensory signal, whereby neural populations reduce their activity after prolonged stimulation. This would mean less residual sensory signal would be available after the cue to supplement VWM activity, predicting a decline in fidelity at higher set sizes. Visual adaptation has previously been successfully accounted for by a type of delayed normalization model in which the sensory signal undergoes a series of linear and nonlinear transformations (Zhou et al., 2019). Such a model could in future be incorporated into DyNR and validated against psychophysical and neural data.”

Carandini, M., & Heeger, D. J. (1994). Summation and division by neurons in primate visual cortex. Science, 264(5163), 1333–1336. https://doi.org/10.1126/science.8191289

Groen, I. I. A., Piantoni, G., Montenegro, S., Flinker, A., Devore, S., Devinsky, O., Doyle, W., Dugan, P., Friedman, D., Ramsey, N. F., Petridou, N., & Winawer, J. (2022). Temporal Dynamics of Neural Responses in Human Visual Cortex. The Journal of Neuroscience, 42(40), 7562–7580. https://doi.org/10.1523/JNEUROSCI.1812-21.2022

Sawamura, H., Orban, G. A., & Vogels, R. (2006). Selectivity of Neuronal Adaptation Does Not Match Response Selectivity: A Single-Cell Study of the fMRI Adaptation Paradigm. Neuron, 49(2), 307–318. https://doi.org/10.1016/j.neuron.2005.11.028

Zhou, J., Benson, N. C., Kay, K., & Winawer, J. (2019). Predicting neuronal dynamics with a delayed gain control model. PLOS Computational Biology, 15(11), e1007484. https://doi.org/10.1371/journal.pcbi.1007484

(2) A second potential weakness is that, in Experiment 1, the authors briefly change the sensory stimulus at the end of the delay (a 'phase shift', Fig. 6A). I believe this is intended to act as a mask. However, I would expect that, in the DyNR model, this should be modeled as a new sensory input (in Experiment 2, 50 ms is plenty of time for the subjects to process the stimuli). One might expect this change to disrupt sensory and memory representations in a very characteristic manner. This seems to make a strong testable hypothesis. Did the authors find evidence for interference from the phase shift?

The phase shift was implemented with the intention of reducing retinal after-effects, essentially acting as a mask for retinal information only; crucially the orientation of the stimulus is unchanged by the phase shift, so from the perspective of the DyNR model, it transmits the same orientation information to working memory as the original stimulus.

If our objective were to model sensory input at the level of individual neurons and their receptive fields, we would indeed need to treat this phase shift as a novel input. Nevertheless, for DyNR, conceived as an idealization of a biological system for encoding orientation information, we can safely assume that visual areas in biological organisms have a sufficient number of phase-sensitive simple cells and phase-indifferent complex cells to maintain the continuity of input to VWM.

When comparing conditions with and without the phase shift of stimuli (Fig S1B), we found performance to be comparable in the perceptual condition (simultaneous presentation) and with the longest delay (1 second), suggesting that the phase shift did not change the visibility or encoding of information into VWM. In contrast, we found strong evidence that observers had access to an additional source of information over intermediate delays when the phase shift was not used. This was evident through enhanced recall performance from 0 ms to 400 ms delay. Based on this, we concluded that the additional source of information available in the absence of a phase shift was accessible immediately following stimulus offset and had a brief duration, aligning with the theoretical concept of retinal afterimages.

(3) It seems odd that the mask does not interrupt sensory processing in Experiment 2. Isn't this the intended purpose of the mask? Should readers interpret this as all masks not being effective in disrupting sensory processing/iconic memory? Or is this specific to the mask used in the experiment?

Visual masks are often described as instantly and completely halting the visual processing of information that preceded the mask. We also anticipated the mask would entirely terminate sensory processing, but our data indicate the effect was not complete (as indicated by model variants in Experiment 2). Nevertheless, we believe we achieved our intended goal with this experiment – we observed a clear modulation of response errors with changing stimulus duration, indicating that the post-stimulus information that survived masking did not compromise the manipulation of stimulus duration. Moreover, the DyNR model successfully accounted for the portion of signal that survived the mask.

We can identify two possible reasons why masking was incomplete. First, it is possible that the continuous report measure used in our experiments is more sensitive than the discrete measures (e.g., forced-choice methods) commonly employed in experiments that found masks to be 100% effective. Second, despite using a flickering white noise mask at full contrast, it is possible that it may not have been the most effective mask; for instance, a mask consisting of many randomly oriented Gabor patches matched in spatial frequency to the stimuli could prove more effective. We decided against such a mask because we were concerned that it could potentially act as a new input to orientation-sensitive neurons, rather than just wiping out any residual sensory activity.

(4) I apologize if I missed it, but the authors did not compare the DyNR model to a model without decaying sensory information for Experiment 1.

We tested two DyNR variants in which the diffusion process was solely responsible for memory fidelity dynamics. These models assumed that the sensory signal terminates abruptly with stimuli offset, and the VWM signal encoding the stimuli was equal to the limit imposed by normalization, independent of the delay duration.

As variants of this model failed to account for the observed response errors both quantitatively (see 'Fixed neural signal' under Model variants) and qualitatively (Figure S3), we decided not to test any more restrictive variants, such as the one without sensory decay and diffusion.

(5) In the current model, selection is considered to be absolute (all or none). However, this need not be the case (previous work argues for graded selection). Could a model where memories are only partially selected, in a manner that is mediated by load, explain the load effects seen in behavior?

Thank you for this point. If attentional selection was partial, it would affect the observers’ efficiency in discarding uncued objects to release allocated resources and encode additional information about the cued item. We and others have previously examined whether humans can efficiently update their VWM when previous items become obsolete. For example, Taylor et al. (2023) showed that observers could efficiently remove uncued items from VWM and reallocate the released resources to new visual information. These findings align with results from other studies (e.g., Ecker, Oberauer, & Lewandowsky, 2014; Kessler & Meiran, 2006; Williams et al., 2013).

Based on these findings, we feel justified in assuming that observers in our current task were capable of fully removing all uncued objects, allowing them to continue the encoding process for the cued orientation that was already partially stored in VWM, such that the attainable limit on representational precision for the cued item equals the maximum precision of VWM.

Partial removal could in principle be modelled in the DyNR model by introducing an additional plateau parameter specifying a maximum attainable precision after the cue. Our concern would be that such a plateau parameter would trade off with the parameter associated with Hick’s law (i.e., cue interpretation time). The former would control the amount of information that can be encoded into VWM, while the latter regulates the amount of sensory information available for encoding. We are wary of adding additional parameters, and hence flexibility, to the model where we do not have the data to sufficiently constrain them.

Ecker, U. K. H., Oberauer, K., & Lewandowsky, S. (2014b). Working memory updating involves item-specific removal. Journal of Memory and Language, 74, 1–15. https://doi.org/10.1016/j.jml. 2014.03.006

Kessler, Y., & Meiran, N. (2006). All updateable objects in working memory are updated whenever any of them are modified: Evidence from the memory updating paradigm. Journal of Experimental Psychology: Learning, Memory, and Cognition, 32, 570–585. https://doi.org/10.1037/0278-7393.32.3.570

Taylor, R., Tomić, I., Aagten-Murphy, D., & Bays, P. M. (2023). Working memory is updated by reallocation of resources from obsolete to new items. Attention, Perception, & Psychophysics, 85(5), 1437–1451. https://doi.org/10.3758/s13414-022-02584-2

Williams, M., & Woodman, G. F. (2012). Directed forgetting and directed remembering in visual working memory. Journal of Experimental Psychology. Learning, Memory, and Cognition, 38(5), 1206–1220. https://doi.org/10.1037/a0027389

(6) Previous work, both from the authors and others, has shown that memories are biased as if they are acted on by attractive/repulsive forces. For example, the memory of an oriented bar is biased away from horizontal and vertical and biased towards diagonals. This is not accounted for in the current model. In particular, this could be one mechanism to generate a non-uniform drift rate over time. As noted in the paper, a non-uniform drift rate could capture many of the behavioral effects reported.

The reviewer is correct that the model does not currently include stimulus-specific effects, although our work on that topic provides a clear template for incorporating them in future (e.g. Taylor & Bays, 2018). Specifically on the question of generating a non-uniform drift, we have another project that currently looks at this exact question (cited in our manuscript as Tomic, Girones, Lengyel, and Bays; in prep.). By examining various datasets with varying memory delays, including the Additional Dataset 1 reported in the Supplementary Information, we found that stimulus-specific effects on orientation recall remain constant with retention time. Specifically, although there is a clear increase in overall error over time, estimation biases remain constant in direction and amplitude, indicating that the bias does not manifest in drift rates (see also Rademaker et al., 2018; Figure S1).

Taylor, R., & Bays, P. M. (2018). Efficient coding in visual working memory accounts for stimulus-specific variations in recall. The Journal of Neuroscience, 1018–18. https://doi.org/10.1523/JNEUROSCI.1018-18.2018

Rademaker, R. L., Park, Y. E., Sack, A. T., & Tong, F. (2018). Evidence of gradual loss of precision for simple features and complex objects in visual working memory. Journal of Experimental Psychology: Human Perception and Performance. https://doi.org/10.1037/xhp0000491

(7) Finally, the authors use AIC to compare many different model variants to the DyNR model. The delta-AICs are high (>10), indicating a strong preference for the DyNR model over the variants. However, the overall quality of fit to the data is not clear. What proportion of the variance in data was the model able to explain? In particular, I think it would be helpful for the reader if the authors reported the variance explained on withheld data (trials, conditions, or subjects).

Thank you for this comment.

Below we report the estimates of r2, representing the goodness of fit between observed data (i.e., RMSE) and the DyNR model predictions.

In Experiment 1, the r2 values between observations and predictions were computed across delays for each set size, yielding the following estimates: r2ss1 = 0.60; r2ss4 = 0.87; r2ss10 = 0.95. Note that lower explained variance for set size 1 arises from both data and model predictions having near-constant precision.

In Experiment 2, we calculated r2 between observations and predictions across presentation durations, separately for each set size, resulting in the following estimates: r2ss1 = 0.88; r2ss4 = 0.71; r2ss10 = 0.70. Note that in this case the decreasing percentage of explained variance with set size is a consequence of having less variability in both data and model predictions with larger set sizes.

While these estimates suggest that the DyNR model effectively fits the psychophysical data, a more rigorous validation approach would involve cross-validation checks across all conditions with a withheld portion of trials. Regrettably, due to the large number of conditions in each experiment, we could only collect 50 trials per condition. We are sceptical that fitting the model to even fewer trials, as necessary for cross-validation, would provide a reliable assessment of model performance.

Minor: It isn't clear to me why the behavioral tasks are shown in Figure 6. They are important for understanding the results and are discussed earlier in the manuscript (before Figure 3). This just required flipping back and forth to understand the task before I could interpret the results.

Thank you for this comment. We have now moved the behavioural task figure to appear early in the manuscript (as Figure 3).

Reviewer #3 (Recommendations For The Authors):

(1) Dynamics of sensory signals during perception

I believe that the modeled sensory signal is a reasonable simplification and different ways to model the decay function are discussed. I would like to ask the authors to discuss the implications of slightly more complex initial sensory transients such as the ones shown in Teeuwen (2021). Specifically for short exposure times, this might be particularly relevant for the model fits as some of the alternative models diverge from the data for short exposures. In addition, the role of feedforward (initial transient?) and feedback signaling (subsequent "plateau" activity) could be discussed. The first one might relate more strongly to sensory signals whereas the latter relates more to top-down attention/recurrent processing/VWM.

Particularly, this latter response might also be sensitive to the number of items present on the screen which leads to a related question pertaining to the limitations of attention during perception. Some work suggests that perception is similarly limited in the amount of information that can be represented concurrently (Tsubomi, 2013). Could the authors discuss the implications of this hypothesis? What happens if maximum sensory amplitude is set as a free parameter in the model?

Tsubomi, H., Fukuda, K., Watanabe, K., & Vogel, E. K. (2013). Neural limits to representing objects still within view. Journal of Neuroscience, 33(19), 8257-8263.

Thank you for this question. Below, we unpack it and answer it point by point.

While we agree our model of the sensory response is justified as an idealization of the biological reality, we also recognise that recent electrophysiological recordings have illuminated intricacies of neuronal responses within the striate cortex, a critical neural region associated with sensory memory (Teeuwen et al, 2021). Notably, these recordings reveal a more nuanced pattern where neurons exhibit an initial burst of activity succeeded by a lower plateau in firing rate, and stimulus offset elicits a second small burst in the response of some neurons, followed by a gradual decrease in activity after the stimulus disappears (Teeuwen et al, 2021).

In general, asynchronous bursts of activity in individual neurons will tend to average out in the population making little difference to predictions of the DyNR model. Synchronized bursts at stimulus onset could affect predictions for the shortest presentations in Exp 2, however the model appears to capture the data very well without including them. We would be wary of incorporating these phenomena into the model without more clarity on their universality (e.g., how stimulus-dependent they are), their significance at the population level (as opposed to individual neurons), and most importantly, their prominence in visual areas outside striate cortex. Specifically, while Teeuwen et al. (2021) described activity in V1, our model does not make strong assumptions about which visual areas are the source of the sensory input to WM. Based on these uncertainties we believe the idealized sensory response is justified for use in our model.

Next, thank you for the comment on feedforward and feedback signals. We have added the following to our manuscript:

“Following onset of a stimulus, the visual signal ascends through visual areas via a cascade of feedforward connections. This feedforward sweep conveys sensory information that persists during stimulus presentation and briefly after it disappears (Lamme et al., 1998). Simultaneously, reciprocal feedback connections carry higher-order information back towards antecedent cortical areas (Lamme and Roelfsema, 2000). In our psychophysical task, feedback connections likely play a critical role in orienting attention towards the cued item, facilitating the extraction of persisting sensory signals, and potentially signalling continuous information on the available resources for VWM encoding. While our computational study does not address the nature of these feedforward and feedback signals, a challenge for future research is to describe the relative contributions of these signals in mediating transmission of information between sensory and working memory (Semedo et al., 2022).”

Lamme, V. A., Supèr, H., & Spekreijse, H. (1998). Feedforward, horizontal, and feedback processing in the visual cortex. Current Opinion in Neurobiology, 8(4), 529–535. https://doi.org/10.1016/S0959-4388(98)80042-1

Lamme, V. A. F., & Roelfsema, P. R. (2000). The distinct modes of vision offered by feedforward and recurrent processing. Trends in Neurosciences, 23(11), 571–579. https://doi.org/10.1016/S0166-2236(00)01657-X

Semedo, J. D., Jasper, A. I., Zandvakili, A., Krishna, A., Aschner, A., Machens, C. K., Kohn, A., & Yu, B. M. (2022). Feedforward and feedback interactions between visual cortical areas use different population activity patterns. Nature Communications, 13(1), 1099. https://doi.org/10.1038/s41467-022-28552-w

Finally, both you and Reviewer 2 raised a similar interesting question regarding capacity limitations of attention during perception Such a limitation could be modelled by freely estimating sensory amplitude and implementing divisive normalization to that signal, similar to how VWM is constrained. We can consider two potential mechanisms through which divisive normalization might be incorporated into sensory processing within the DyNR model.

The first possibility involves assuming that normalization is pre-attentive. In this scenario, the sensory activity of each object would be rescaled at the lowest level of sensory processing, occurring before the allocation of attentional or VWM resources. One strong prediction of such an implementation is that recall error in the simultaneous cue condition (Experiment 1) should vary with set size. However, this prediction is inconsistent with the observed data, which failed to show a significant difference between set sizes, and is more closely aligned with the hypothesis of no-difference (F(2,18) = 1.26, p = .3, η2 = .04, BF10 = 0.47). On that basis, we anticipate that introducing normalization as a pre-attentive mechanism would impair the model fit.

An alternative scenario is to consider normalization as post-attentive. In the simultaneous cueing condition, only one item is attended (i.e., the cued one), regardless of the displayed set size. Here, we would expect normalized activity for a single item, regardless of the number of presented objects, which would then be integrated into VWM. This expanded DyNR model with post-attentive normalization would make exactly the same predictions as the proposed DyNR for recall fidelity, so distinguishing between these models would not be possible based on working memory experiments.

To acknowledge the possibility that sensory signals could undergo divisive normalization and to motivate future research, we have added the following to our manuscript:

“As well as being implicated in higher cognitive processes including VWM (Buschman et al, 2011; Sprague et al., 2014), divisive normalization has been shown to be widespread in basic sensory processing (Bonin et al., 2005; Busse et al., 2009; Ni et al., 2017). The DyNR model presently incorporates the former but not the latter type of normalization. While the data observed in our experiments do not provide evidence for normalization of sensory signals (note comparable recall errors across set size in the simultaneous cue condition of Experiment 1), this may be because sensory suppressive effects are localized and our stimuli were relatively widely separated in the visual field: future research could explore the consequences of sensory normalization for recall from VWM using, e.g., centre-surround stimuli (Bloem et al., 2018).”

Bloem, I. M., Watanabe, Y. L., Kibbe, M. M., & Ling, S. (2018). Visual Memories Bypass Normalization. Psychological Science, 29(5), 845–856. https://doi.org/10.1177/0956797617747091

Bonin, V., Mante, V., & Carandini, M. (2005). The Suppressive Field of Neurons in Lateral Geniculate Nucleus. The Journal of Neuroscience, 25(47), 10844–10856. https://doi.org/10.1523/JNEUROSCI.3562-05.2005

Buschman, T. J., Siegel, M., Roy, J. E., & Miller, E. K. (2011). Neural substrates of cognitive capacity limitations. Proceedings of the National Academy of Sciences, 108(27), 11252–11255. https://doi.org/10.1073/pnas.1104666108

Busse, L., Wade, A. R., & Carandini, M. (2009). Representation of Concurrent Stimuli by Population Activity in Visual Cortex. Neuron, 64(6), 931–942. https://doi.org/10.1016/j.neuron.2009.11.004

Ni, A. M., & Maunsell, J. H. R. (2017). Spatially tuned normalization explains attention modulation variance within neurons. Journal of Neurophysiology, 118(3), 1903–1913. https://doi.org/10.1152/jn.00218.2017

Sprague, T. C., Ester, E. F., & Serences, J. T. (2014). Reconstructions of Information in Visual Spatial Working Memory Degrade with Memory Load. Current Biology, 24(18), 2174–2180. https://doi.org/10.1016/j.cub.2014.07.066

(2) Effectivity of retro-cues at long delays

Can the authors discuss how cues presented at long delays (>1000 ms) can still lead to increased memory fidelity when sensory signals are likely to have decayed? A list of experimental work demonstrating this can be found in Souza & Oberauer (2016).

Souza, A. S., & Oberauer, K. (2016). In search of the focus of attention in working memory: 13 years of the retro-cue effect. Attention, Perception, & Psychophysics, 78, 1839-1860.

The increased memory fidelity observed with longer delays between memory array offset and cue does not result from integrating available sensory signals into VWM because the sensory signal would have completely decayed by that time. Instead, research so far has indicated several alternative mechanisms that could lead to higher recall precision for cued items, and we can briefly summarize some of them, which are also reviewed in more detail in Souza and Oberauer (2016).

One possibility is that, after a highly predictive retro-cue indicates the to-be-tested item, uncued items can simply be removed from VWM. This could result in decreased interference for the cued item, and consequently higher recall precision. Secondly, the retro-cue could also indicate which item can be selectively attended to, and thereby differentially strengthening it in memory. Furthermore, the retro-cue could allow evidence to accumulate for the target item ahead of decision-making, and this could increase the probability that the correct information will be selected for response. Finally, the retro-cued stimulus could be insulated from interference by subsequent visual input, while the uncued stimuli may remain prone to such interference.

A neural account of this retro-cue effect based on the original neural resource model has been proposed in Bays & Taylor, Cog Psych, 2018. However, as we did not use a retro-cue design in the present experiments, we have decided not to elaborate on this in the manuscript.

(3) Swap errors

I am somewhat surprised by the empirically observed and predicted pattern of swap errors displayed in Figure S2. For set size 10, swap probability does not consistently increase with the duration of the retention interval, although this was predicted by the author's model. At long intervals, swap probability is significantly higher for large compared to small set sizes, which also seems to contrast with the idea of shared, limited VWM resources. Can the authors provide some insight into why the model fails to reproduce part of the behavioral pattern for swap errors? The sentence in line 602 might also need some reconsideration in this regard.

Determining the ground truth for swap errors poses a challenge. The prevailing approach has been to employ a simpler model that estimates swap errors, such as a three-component mixture model, and use those estimates as a proxy for ground truth. However, this method is not without its shortcomings. For example, the variability of swap frequency estimates tends to increase with variability in the report feature dimension (here, orientation). This is due to the increasing overlap of response probability distributions for swap and non-swap responses. Consequently, the discrepancy between any two methods of swap estimation is most noticeable when there is substantial variability in orientation reports (e.g., 10 items and long delay or short exposure).

When modelling swap frequency in the DyNR model, our aim was to provide a parsimonious account of swap errors while implementing similar dynamics in the spatial (cue) feature as in the orientation (report) feature. This parametric description captured the overall pattern of swap frequency with set size and retention and encoding time, but is still only an approximation of the predictions if we fully modelled memory for the conjunction of cue and report features (as in e.g. Schneegans & Bays, 2017; McMaster et al, 2020).

We expanded the existing text in the section ‘Representational dynamics of cue-dimension features’ of our manuscript:

“… Although we did not explicitly model the neural signals representing location, the modelled dynamics in the probability of swap errors were consistent with those of the primary memory feature. We provided a more detailed neural account of swap errors in our earlier works that is theoretically compatible with the DyNR model (McMaster et al., 2020; Schneegans & Bays, 2017).

The DyNR model successfully captured the observed pattern of swap frequencies (intrusion errors). The only notable discrepancy between DyNR and the three-component mixture model (Fig. S2) arises with the largest set size and longest delay, although with considerable interindividual variability. As the variability in report-dimension increases, the estimates of swap frequency become more variable due to the growing overlap between the probability distributions of swap and non-swap responses. This may explain apparent deviations from the modelled swap frequencies with the highest set size and longest delay where orientation response variability was greatest. “

McMaster, J. M. V., Tomić, I., Schneegans, S., & Bays, P. M. (2022). Swap errors in visual working memory are fully explained by cue-feature variability. Cognitive Psychology, 137, 101493. https://doi.org/10.1016/j.cogpsych.2022.101493

Schneegans, S., & Bays, P. M. (2017). Neural Architecture for Feature Binding in Visual Working Memory. The Journal of Neuroscience, 37(14), 3913–3925. https://doi.org/10.1523/JNEUROSCI.3493-16.2017

(4) Direct sensory readout

The model assumes that readout from sensory memory and from VWM happens with identical efficiency. Currently, we don't know if these two systems are highly overlapping or are fundamentally different in terms of architecture and computation. In the case of the latter, it might be less reasonable to assume that information readout would happen at similar efficiencies, as it is currently assumed in the manuscript. Perhaps the authors could briefly discuss this possibility.

In the direct sensory read-out model, we did not explicitly model the efficiency of readout from either sensory or VWM store. However, the distinctive prediction of this model is that the precision of recall changes exponentially with delay at every set size, including one item. This prediction does not depend on the relative efficiency of readout from sensory and working memory, but only on the principle that direct readout from sensory memory bypasses the capacity limit on working memory. This prediction is inconsistent with the pattern of results observed in Experiment 1, where early cues did not show a beneficial effect on recall error for set size 1. While the proposal raised by the reviewer is intriguing, even if we were to model the process of readout from both the sensory and VWM stores with different efficiencies, the direct read-out model could not account for the near-constant recall error with delay for set size one.

(5) Encoding of distractors

One of the model assumptions is that, for simultaneous presentations of memory array and cue only the cued feature will be encoded. Previous work has suggested that participants often accidentally encode distractors even when they are cued before memory array onset (Vogel 2005). Given these findings, how reasonable is this assumption in the authors' model?

Vogel, E. K., McCollough, A. W., & Machizawa, M. G. (2005). Neural measures reveal individual differences in controlling access to working memory. Nature, 438(7067), 500-503.

Although previous research suggested that observers can misinterpret the pre-cue and encode one of the uncued items, our results argue against this being the case in the current experiment. Such encoding failures would manifest in overall recall error, resulting in a gradient of error with set size, owing to the presence of more adjacent distractors in larger set sizes. However, when we compared recall errors between set sizes in the simultaneous cue condition, we did not find a significant difference between set sizes, and moreover, our results were more likely under the hypothesis of no-difference (F(2,18) = 1.26, p = .3, η2 = .04, BF10 = 0.47). If observers occasionally encoded and reported one of the uncued items in the simultaneous cue condition, those errors were extremely infrequent and did not affect the overall error distributions.

eLife assessment

This study presents important insights into the dynamical process whereby sensory information is converted from stimulus-driven activity to a working memory representation from which the information can be recalled later. The evidence supporting the claims is convincing, using detailed fits and model-comparison techniques applied to new and existing psychophysical data sets to evaluate a wide variety of potential mechanisms. The overall conclusion, that iconic memory and working memory are not distinct mechanisms but rather two slightly different regimes of the same circuitry, will be of interest to neuroscientists and psychologists studying sensory systems and/or working memory.

Reviewer #2 (Public Review):

Summary:

Previous work has shown subjects can use a form of short-term sensory memory, known as 'iconic memory', to accurately remember stimuli over short periods of time (several hundred milliseconds). Working memory maintains representations for longer periods of time but is strictly limited in its capacity. While it has long been assumed that sensory information acts as the input to working memory, a process model of this transfer has been missing. To address this, Tomic and Bays present the Dynamic Neural Resource (DyNR) model. The DyNR model captures the dynamics of processing sensory stimuli, transferring that representation into working memory, the diffusion of representations within working memory, and the selection of a memory for report.

The DyNR model captures many of the effects observed in behavior. Most importantly, psychophysical experiments found the greater the delay between stimulus presentation and the selection of an item from working memory, the greater the error. This effect also depended on working memory load. In the model, these effects are captured by the exponential decay of sensory representations (i.e., iconic memory) following the offset of the stimulus. Once the selection cue is presented, residual information in iconic memory can be integrated into working memory, improving the strength of the representation and reducing error. This selection process takes time, and is slower for larger memory loads, explaining the observation that memory seems to decay instantly. The authors compare the DyNR model to several variants, demonstrating the importance of persistence of sensory information in iconic memory, normalization of representations with increasing memory load, and diffusion of memories over time.

Strengths:

The manuscript provides a convincing argument for the interaction of iconic memory and working memory, as captured by the DyNR model. The analyses are cutting-edge and the results are well captured by the DyNR model. In particular, a strength of the manuscript is the comparison of the DyNR model to several alternative variants.

The results provide a process model for interactions between iconic memory and working memory. This will be of interest to neuroscientists and psychologists studying working memory. I see this work as providing a foundation for understanding behavior in continuous working memory tasks, from either a mechanistic, neuroscience, perspective or as a high-water mark for comparison to other psychological process models.

Finally, the manuscript is well written. The DyNR model is nicely described and an intuition for the dynamics of the model are clearly shown in Figures 2 and 4.

Weaknesses:

The manuscript appropriately acknowledges and addresses several minor weaknesses that are due to the limited ability of the approach to disambiguate underlying neural mechanisms. Nevertheless, the manuscript adds significant value to the literature on working memory.

Reviewer #3 (Public Review):

Summary

The authors set out to formally contrast several theoretical models of working memory, being particularly interested in comparing the models regarding their ability to explain cueing effects at short cue durations. These benefits are traditionally attributed to the existence of a high capacity, rapidly decaying sensory storage which can be directly read out following short latency retro-cues. Based on the model fits, the authors alternatively suggest that cue-benefits arise from a freeing of working memory resources, which at short cue latencies can be utilized to encode additional sensory information into VWM.

A dynamic neural population model consisting of separate sensory and VWM populations was used to explain temporal VWM fidelity of human behavioral data collected during several working memory tasks. VWM fidelity was probed at several timepoints during encoding, while sensory information was available and maintenance, when sensory information was no longer available. Furthermore, set size and exposure durations were manipulated to disentangle contributions of sensory and visual working memory.

Overall, the model explained human memory fidelity well, accounting for set size, exposure time, retention time, error distributions and swap errors. Crucially the model suggests that recall at short delays is due to post-cue integration of sensory information into VWM as opposed to direct readout from sensory memory. The authors formally address several alternative theories, demonstrating that models with reduced sensory persistence, direct readout from sensory memory, no set-size dependent delays in cue processing and constant accumulation rate provide significantly worse fits to the data.

I congratulate the authors for this rigorous scientific work. All my remarks were thoroughly addressed.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Zhang et al., investigated the relationship between monocular and binocular responses of V1 superficial-layer neurons using two-photon calcium imaging. They found a strong relationship in their data: neurons that exhibited a greater preference for one eye or the other (high ocular dominance) were more likely to be suppressed under binocular stimulation, whereas neurons that are more equivalently driven by each other (low ocular dominance) were more likely to be enhanced by binocular stimulation. This result chiefly demonstrates the relationship between ocular dominance and binocular responses in V1, corroborating what has been shown previously using electrophysiological techniques but now with greater spatial resolution (albeit less temporal resolution). The binocular responses were well-fitted by a model that institutes divisive normalization between the eyes that accounts for both the suppression and enhancement phenomena observed in the subpopulation of binocular neurons. In so doing, the authors reify the importance of incorporating ocular dominance in computational models of binocular combination.

The conclusions of this paper are mostly well supported by the data, but there are some limitations of the methodology that need to be clarified, and an expansion of how the results relate to previous work would better contextualize these important findings in the literature.

Strengths:

The two-photon imaging technique used to resolve the activity of individual neurons within intact brain tissue grants a host of advantages. Foremost, two-photon imaging confers considerably high spatial resolution. As a result, the authors were able to sample and analyze the activity from thousands of verified superficial-layer V1 neurons. The animal model used, awake macaques, is also highly relevant for the study of binocular combination. Macaques, like humans, are binocular animals, meaning they have forward-facing eyes that confer overlapping visual fields. Importantly, macaque V1 is organized into cortical columns that process specific visual features from the separate eyes just like in humans. In combination with a powerful imaging technique, this allowed the authors to evaluate the monocular and binocular response profiles of V1 neurons that are situated within neighboring ocular dominance columns, a novel feat. To this aim, the approach was well-executed and should instill further confidence in the notion that V1 neurons combine monocular information in a manner that is dependent on the strength of their ocular dominance.

Weaknesses:

While two-photon imaging provides excellent spatial resolution, its temporal resolution is often lower compared to some other techniques, such as electrophysiology. This limits the ability to study the fast dynamics of neuronal activity, a well-understood trade-off of the method. The issue is more so that the authors draw comparisons to electrophysiological studies without explicit appreciation of the temporal difference between these techniques. In a similar vein, two-photon imaging is limited spatially in terms of cortical depth, preferentially sampling from neurons in layers 2/3. This limitation does not invalidate any of the interpretations but should be considered by readers, especially when making comparisons to previous electrophysiological reports using microelectrode linear arrays that sample from all cortical layers. Indeed, it is likely that a complete picture of early cortical binocular processing will require high spatial resolution (i.e., sampling from neurons in neighboring ocular dominance columns, from pia mater to white matter) at the biophysically relevant timescales (1ms resolution, capturing response dynamics over the full duration of the stimulus presentation, including the transient onset and steady-state periods).

To address the same concern from all three reviewers, we discussed the technical limitations of two photon calcium imaging at the end of Discussion, including limited imaging depth, low temporal resolution, and nonlinearity. The relevant texts are copied here:

(Ln 304) “Limitations of the current study

Although capable of sampling a large number of neurons at cellular resolution and with low sampling bias, two-photon calcium imaging has its known limitations that may better make it a complementary research tool to electrophysiological recordings.

For example, two-photon imaging can only sample neurons from superficial-layers, while binocular neurons also exist in deeper layers, and even neurons in the input layer are affected by feedback from downstream binocular neurons to exhibit binocular response properties (Dougherty, Cox, Westerberg, & Maier, 2019). Furthermore, calcium signals are relatively slow and cannot reveal the fast dynamics of neuronal responses. Due to these spatial and temporal limitations, a more complete picture of the neuronal mechanisms underlying binocular combination of monocular responses may come from studies using both technologies.

In addition, calcium signals may exaggerate the nonlinear properties of neurons. Although calcium signals indicated by GCaMP5, our favored choice of calcium indicator, displays a linear relationship to neuronal spike rates within a range of 10-150 Hz (Li, Liu, Jiang, Lee, & Tang, 2017), weak and strong signals out of this range are more nonlinear, and may appear poorer and stronger, respectively, than electrode-recorded effects. Consequently, the differences in population responses between monocular and binocular stimulations revealed by this study might be less pronounced.”

(Recommendations For The Authors):

Overall, my main suggestion for the authors to improve the paper is to revise some of the interpretations of their results in relation to previous research. The purpose of the present study was to illustrate a more complete picture of the binocular combination of monocular responses by taking into consideration the ocular dominance of V1 cells (lines 34-36). A study published earlier this year had an identical purpose (Mitchell et al., Current Biology, 2023) and arrived at a highly similar conclusion (and also applied divisive normalization to fit their data). I would ask that this paper be mentioned in the introduction and discussed.

The Mitchell et al 2023 paper is added to the Introduction and Discussion:

(Ln 50) “In addition (to the Dougherty et al 2019 paper from the same group), Mitchell, Carlson, Westerberg, Cox, and Maier (2023) reported that binocular combination of monocular stimuli with different contrasts is also affected by neurons’ eye preference.”

(Ln 286) “The critical roles of ocular dominance have been largely overlooked by extant binocular vision models to our knowledge, except that Anderson and Movshon (1989) demonstrated that a model consisting of multiple ocular dominance channels can better explain their psychophysical adaptation data, and that Mitchell et al. (2023) revealed that binocular combination of different contrasts presented to different eyes are affected by neurons’ ocularity preference.”

Nevertheless, the results of the present study are very valuable. They add substantial spatial resolution and sophisticated relational analysis of monocular and binocular responses that Mitchell et al., 2023 did not include. Therefore, my suggestion is to emphasize the advantages of two-photon imaging in the introduction, focusing on the ability to image neurons in neighboring ocular dominance columns. The rigorous modeling of the relationship between nearby neurons with a range of eye preferences, in tandem with the incredible yield of two-photon imaging, is what sets this paper apart from previous electrophysiological work.

The finding that binocular responses were dependent on ocular dominance is largely consistent with previous electrophysiological results. However, there should be a paragraph in the discussion section that speaks to the limitations of comparing two-photon imaging data to electrophysiological data. Namely, there are two limitations:

(1) These two techniques confer different temporal resolutions. It is conceivable that some of the electrophysiology relationships (for example, described by Dougherty et al., 2019) may be dependent on the temporal window over which the data was averaged, typically over 50-100ms around stimulus onset, or 100-250ms comprising the neurons' sustained response to the stimulus. This possible explanation of the difference in obtained results would be especially useful for the discussion paragraph starting at line 232. It would also be helpful to readers for there to be some mention of the advantage of having high temporal resolution (i.e., the benefits of electrophysiology) since (a) recent work has distinguished between sequential stages of binocular combination (Cox et al., 2019) and (b) modern models of V1 neurons emphasize recurrent feedback to explain V1 temporal dynamics (see Heeger et al., 2019; Rubin et al., 2015), which could prove to be relevant for combination of stimuli in the two eyes (Fleet et al., 1997).

Our discussion regarding the technical limitations of 2-p calcium imaging has been listed earlier. Specific to the Dougherty et 2019 paper, we added the following discussion to address the issue of temporal resolution difference between two technologies.

(Ln 266) “In addition, it is unclear whether the discrepancies are caused by different temporal resolutions of electrode recording and calcium imaging. The results of Dougherty et al. (2019) represent changes of neuronal spike activities over a period of approximately 50-200 ms after the stimulus onset, which may reflect the sustained neuronal responses to the stimulus and possible feedback signals. Calcium signals are much slower and indicative of the aggregated neuronal responses over a longer period (up to 1000 ms in the current study). They should have smeared, rather than exaggerated, the differences between monocular and binocular responses, although we cannot exclude the possibility that some neuronal response changes beyond 200 ms are responsible for the discrepancies.”

(2) The sample of V1 neurons in this study is limited to cells in the most superficial layers of the cortex (layers 2/3). This limitation is, of course, well understood, but it should be mentioned at least in the context of studying the formative mechanisms of binocular combination in V1 (since we know that binocular neurons also exist in layers 5/6, and there is now substantial evidence that even layer 4 neurons are not as "monocular" as we previously thought (Dougherty et al., 2019)).

See our discussion regarding the technical limitations of 2-p calcium imaging listed earlier.

In short, I believe the paper would be improved by (1) adding the above citations in the appropriate places, (2) acknowledging in the introduction that this question has been investigated electrophysiologically but emphasizing the advantages of two-photon imaging, and (3) adding a paragraph to the discussion section that discusses the temporal and spatial limitations when using two-photon imaging to study binocular combination, particularly when comparing the results to electrophysiology.

Reviewer #2 (Public Review):

Summary:

This study examines the pattern of responses produced by the combination of left-eye and right-eye signals in V1. For this, they used calcium imaging of neurons in V1 of awake, fixating monkeys. They take advantage of calcium imaging, which yields large populations of neurons in each field of view. With their data set, they observe how response magnitude relates to ocular dominance across the entire population. They analyze carefully how the relationship changed as the visual stimulus switched from contra-eye only, ipsi-eye only, and binocular. As expected, the contra-eye-dominated neurons responded strongly with a contra-eye-only stimulus. The ipsi-eye-dominated neurons responded strongly with an ipsi-eye-only stimulus. The surprise was responses to a binocular stimulus. The responses were similarly weak across the entire population, regardless of each neuron's ocular dominance. They conclude that this pattern of responses could be explained by interocular divisive normalization, followed by binocular summation.

Strengths:

A major strength of this work is that the model-fitting was done on a large population of simultaneously recorded neurons. This approach is an advancement over previous work, which did model-fitting on individual neurons. The fitted model in the manuscript represents the pattern observed across the large population in V1, and washes out any particular property of individual neurons. Given the large neuronal population from which the conclusion was drawn, the authors provide solid evidence supporting their conclusion. They also observed consistency across 5 fields of view.

The experiments were designed and executed appropriately to test their hypothesis. Their data support their conclusion.

Weaknesses:

One weakness of their study is that calcium signals can exaggerate the nonlinear properties of neurons. Calcium imaging renders poor responses poorer and strong responses stronger, compared to single-unit recording. In particular, the dramatic change in the population response between monocular stimulation and binocular stimulation could actually be less pronounced when measured with single-unit recording methods. This means their choice of recording method could have accidentally exaggerated the evidence of their finding.

We discussed the nonlinearity of calcium signals as part of the technical limitations of 2-p imaging calcium. The calcium indicator we use, GCaMP5, has a reasonable range of linear relationship with spike rates. But out of this range, the nonlinearity is indeed a concern.

(Ln 314) “In addition, calcium signals may exaggerate the nonlinear properties of neurons. Although signals indicated by GCaMP5, our favored choice of calcium indicator, displays a linear relationship to neuronal spike rate within a range of 10-150 Hz (Li et al., 2017), weak and strong signals out of this range are more nonlinear, and may appear poorer and stronger, respectively, than electrode-recorded effects. Consequently, the changes in population responses between monocular and binocular stimulations revealed by this study might be less pronounced.”

The implication of their finding is that strong ocular dominance is the result of release from interocular suppression by a monocular stimulus, rather than the lack of binocular combination as many traditional studies have assumed. This could significantly advance our understanding of the binocular combination circuitry of V1. The entire population of neurons could be part of a binocular combination circuitry present in V1.

This is a very good insight. We added the following sentences to the end of the first paragraph of Discussion:

(Ln 242) “These findings implicate that at least for neurons in superficial layers of V1, significant ocular dominance may result from a release of interocular suppression during monocular stimulation, an unusual viewing condition as our vision is typically binocular, rather than a lack of binocular combination of inputs from upstream monocular neurons.”

(Recommendations For The Authors):

Line 150: "To model interocular response suppression, responses from each eye in Eq. 2 were further normalized by an interocular suppression factor wib or wcb," I recommend the authors improve their explanation of how they arrived at Eq. 3 from Eq. 2. As it stands, my impression is that they have one model for the responses to monocular stimulation, and another model for the responses to binocular stimulation. What I think is missing is that both equations are derived from the same model. Monocular stimulation is a situation in which the stimulus in one eye's contrast is zero. Could the authors clarify whether this situation produces an interocular suppression of zero, and how that leads to Eq. 2?

We rewrote the modeling part to show that Equations 1-3 are sequential steps of development for the same model. We also added a brief paragraph to discuss how Eq. 3 could lead to Eq. 2 under monocular viewing:

(Ln 166) “Although not shown in Eq. 3, we also assumed that the nonlinear exponent b also depends on the contrast of the stimulus presented to the other eye (i.e., Sc or Si). Consequently, when Sc or Si = 0 under monocular stimulation, Rc or Ri = 0 (Eq. 1), and interocular suppression wib or wcb = 1, so Eq. 3 changes back to Eq. 2. It is only when Sc and Si are equal and close to 1, as in the current study, that interocular suppression and binocular combination would be in the current Eq. 3 format.”

Line 225: "However, individually, compared to monocular responses, responses of monocular neurons more preferring the stimulated eye are actually suppressed, and only responses of binocular neurons are increased by binocular stimulation." This sentence is difficult to follow. I recommend the authors improve clarity by breaking up the sentence into several sentences. If I understand correctly, they summarize the pattern in the data that is indicative of interocular divisive normalization, i.e., their final conclusion.

This sentence no longer exists in the Discussion.

Line 426: "Third, for those showing significant orientation difference, the trial-based orientation responses of each neuron were fitted with a Gaussian model with a MATLAB nonlinear least squares function:" The choice of using a Gaussian function to fit orientation tuning was probably suboptimal. A Gaussian function provides an adequate fit only for neurons whose tuning is very sharp. The responses outside of the peak fall down to the baseline and the two ends meet. Otherwise, the two ends do not meet. An adequate fit would be achieved with a function of a circular variable, which wraps around 180 deg. I recommend using a Von Mises function for fitting orientation tuning.

We agree with the reviewer that the Von Mises function is more accurate than Gaussian for fitting orientation tuning functions. Indeed we are using it to fit orientation tuning of V4 neurons, many of which have two peaks. For the current V1 data, the differences between Von Mises and Gaussian fittings are very small, as shown in the orientation functional maps from three macaques below. Because we also use the same Gaussian fitting of orientation tuning in several published and current under-review papers, we prefer to keep the Gaussian fitting results in the manuscript.

Author response image 1.

Reviewer #3 (Public Review):

The authors have made simultaneous recordings of the responses of large numbers of neurons from the primary visual cortex using optical two-photon imaging of calcium signals from the superficial layers of the cortex. Recordings were made to compare the responses of the cortical neurons under normal binocular viewing of a flat screen with both eyes open and monocular viewing of the same screen with one eye's view blocked by a translucent filter. The screen displayed visual stimuli comprising small contrast patches of Gabor function distributions of luminance, a stimulus that is known to excite cortical neurons.

This is an important data set, given the large numbers of neurons recorded. The authors present a simple model to explain the binocular combination of neuronal signals from the right and left eyes.

The limitations of the paper as written are as follows. These points can be addressed with some additional analysis and rewriting of sections of the paper. No new experimental data need to be collected.

(1) The authors should acknowledge the fact that these recordings arise from neurons in the superficial layers of the cortex. This limitation arises from the usual constraints on optical imaging in the macaque cortex. This means that the sample of neurons forming this data set is not fully representative of the population of binocular neurons within the visual cortex. This limitation is important in comparing the outcome of these experiments with the results from other studies of binocular combination, which have used single-electrode recording. Electrode recording will result in a sample of neurons that is drawn from many layers of the cortex, rather than just the superficial layers.

See our discussion regarding the technical limitations of 2-p calcium imaging listed earlier.

(2) Single-neuron recording of binocular neurons in the primary visual cortex has shown that these neurons often have some spontaneous activity. Assessment of this spontaneous level of firing is important for accurate model fitting [1]. The paper here should discuss the level of spontaneous neuronal firing and its potential significance.

We have noticed previously that at non-optimal spatial frequencies, calcium responses to a moving Gabor grating are close to zero (Guan et al., Prog Neurobiology, 2021, Fig. 1B), but we cannot tell whether this is due to calcium response nonlinearity, or a close-to-zero level of spontaneous neuronal activity. Prince et al (2002) reported low spontaneous responses of V1 neurons with moving grating stimuli (e.g., about 3 spikes/sec in one exemplar neuron, their Fig. 1B), so this appears not a big effect. In our data fitting, we do have an orientation-unspecific component in the Gaussian model, which represents the neuronal response at a non-preferred orientation, but not necessarily the spontaneous activity.

(3) The arrangements for visual stimulation and comparison of binocular and monocular responses mean that the stereoscopic disparity of the binocular stimuli is always at zero or close to zero. The animal's fixation point is in the centre of a single display that is viewed binocularly. The fixation point is, by definition, at zero disparity. The other points on the flat display are also at zero disparity or very close to zero because they lie in the same depth plane. There will be some small deviations from exactly zero because the geometry of the viewing arrangements results in the extremities of the display being at a slightly different distance than the centre. Therefore, the visual stimulation used to test the binocular condition is always at zero disparity, with a slight deviation from zero at the edges of the display, and never changes. [There is a detail that can be ignored. The experimenters tested neurons with visual stimulation at different real distances from the eyes, but this is not relevant here. Provided the animals accurately converged their eyes on the provided binocular fixation point, then the disparity of the visual stimuli will always be at or close to zero, regardless of viewing distance in these circumstances.] However, we already know from earlier work that neurons in the visual cortex exhibit a range of selectivity for binocular disparity. Some neurons have their peak response at non-zero disparities, representing binocular depths nearer than the fixation depth or beyond it. The response of other neurons is maximally suppressed by disparities at the depth of the fixation point (so-called Tuned Inhibitory [TI] neurons). The simple model and analysis presented in the paper for the summation of monocular responses to predict binocular responses will perform adequately for neurons that are tuned to zero disparity, so-called tuned excitatory neurons [TE], but is necessarily compromised when applied to neurons that have other, different tuning profiles. Specifically, when neurons are stimulated binocularly with a non-preferred disparity, the binocular response may be lower than the monocular response[2, 3]. This more realistic view of binocular responses needs to be considered by the authors and integrated into their modelling.

We agree and include the following texts when discussing the future work:

(Ln 298) “In addition, in our experiments, binocular stimuli were presented with zero disparity, which best triggered the responses of neurons with zero-disparity tuning. A more realistic model of binocular combination also requires the consideration of neurons with other disparity-tuning profiles.”

(4) The data in the paper show some features that have been reported before but are not captured by the model. Notably for neurons with extreme values of ocular dominance, the binocular response is typically less than the larger of the two monocular responses. This is apparent in the row of plots in Figure 2D from individual animals and in the pooled data in Figure 2E. Responses of this type are characteristic of tuned inhibitory [TI] neurons[2]. It is not immediately clear why this feature of the data does not appear in the summary and analysis in Figure 3.

This difference is indeed captured by the model, which can be more easily appreciated in Fig. 4A where monocular and binocular model simulations are plotted in the same panel. In the text, we also wrote: (Ln 195) “It is apparent that binocular responses cannot be explained by the sum of monocular responses, as binocular responses are substantially lower than the summed monocular responses for both monocular and binocular neurons. Nor can binocular responses be explained by the responses to the preferred eye, as binocular responses are also lower than those to the preferred eye (the larger of the two monocular responses) for monocular neurons.”

The paper text states that the responses were "first normalized by the median of the binocular responses". This will certainly get rid of this characteristic of the data, but this step needs better justification, or an amendment to the main analysis is needed.

The relevant sentence has been rewritten as “Monocular and binocular data of each FOV/depth, as well as the pooled data, were first normalized by the respective median of the binocular responses of all neurons in the same FOV/depth.” This normalization would render the overall binocular responses to be around unity, for the purpose of facilitating comparisons among all FOV/depth, but it would not affect the overall characteristic of the data.

In the present form, the model and analysis do not appear to fit the data in Figure 2 as accurately as needed.

Thanks for pointing out the problem, as data fitting for FOV C_270 and the pooled data were especially inaccurate. The issue has been mostly fixed when each datum was weighted by its standard deviation (please see the updated Fig. 3).

eLife assessment

Overall, the reviewers found the significance of the work valuable to the field of visual neuroscience, particularly given the large data set and strength of the method used that allowed for spatial analysis of neuronal responses in macaque V1. The evidence was deemed compelling, owing in part to the consistency of responses across animals and the fitness of modeling. The authors have addressed the major comments from reviewers and improved the manuscript through relation to prior literature and addressing specific limitations of the method used.

Reviewer #1 (Public Review):

Summary:

Zhang et al., investigated the relationship between monocular and binocular responses of V1 superficial-layer neurons using two-photon calcium imaging. They found a strong relationship in their data: neurons that exhibited a greater preference for one eye or the other (high ocular dominance) were more likely to be suppressed under binocular stimulation, whereas neurons that are more equivalently driven by each other (low ocular dominance) were more likely to be enhanced by binocular stimulation. This result chiefly demonstrates the relationship between ocular dominance and binocular responses in V1, corroborating what has been shown previously using electrophysiological techniques with now much finer spatial resolution. The binocular responses were well-fitted by a model that institutes divisive normalization between the eyes that accounts for both the suppression and enhancement phenomena observed in the subpopulation of binocular neurons. In so doing, the authors reify the importance of incorporating ocular dominance in computational models of binocular combination.

The conclusions of this paper are well supported by the data. The authors deftly contextualize these important findings in the literature while also acknowledging the limitations of the methodology employed. Future work would do well to combine the spatial power of 2P imaging with the temporal power of electrophysiology to assess ocular dominance-dependent binocular combination across the V1 laminar microcircuit.

Strengths:

The two-photon imaging technique used to resolve the activity of individual neurons within intact brain tissue grants a host of advantages. Foremost, two-photon imaging confers considerably high spatial resolution. As a result, the authors were able to sample and analyze the activity from thousands of verified superficial-layer V1 neurons. The animal model used, awake macaques, is also highly relevant for the study of binocular combination. Macaques, like humans, are binocular animals, meaning they have forward-facing eyes that confer overlapping visual fields. Importantly, macaque V1 is organized into cortical columns that process specific visual features from the separate eyes just like in humans. In combination with a powerful imaging technique, this allowed the authors to evaluate the monocular and binocular response profiles of V1 neurons that are situated within neighboring ocular dominance columns, a novel feat. To this aim, the approach was well-executed and should instill confidence in the notion that V1 neurons combine monocular information in a manner that is dependent on the strength of their ocular dominance.

Weaknesses:

This study suffers no major weaknesses. The authors address the limitations of the methodology and have calibrated the interpretations accordingly.

Reviewer #2 (Public Review):

Summary:

This study examines the pattern of responses produced by the combination of left-eye and right-eye signals in V1. For this, they used calcium imaging of neurons in V1 of awake, fixating monkeys. They take advantage of calcium imaging, which yields large populations of neurons in each field of view. With their data set, they observe how response magnitude relates to ocular dominance across the entire population. They analyze carefully how the relationship changed as the visual stimulus switched from contra-eye only, ipsi-eye only, and binocular. As expected, the contra-eye dominated neurons responded strongly with a contra-eye only stimulus. The ipsi-eye dominated neurons responded strongly with an ipsi-eye only stimulus. The surprise was responses to a binocular stimulus. The responses were similarly weak across the entire population, regardless of each neuron's ocular dominance. They conclude that this pattern of responses could be explained by interocular divisive normalization, followed by binocular summation.

Strengths:

A major strength of this work is that the model-fitting was done on a large population of simultaneously recorded neurons. This approach is an advancement over previous work, which did model-fitting on individual neurons. The fitted model in the manuscript represents the pattern observed across the large population in V1, and washes out any particular property of individual neurons. Given the large neuronal population from which the conclusion was drawn, the authors provide solid evidence supporting their conclusion. They also observed consistency across 5 field of views.

The experiments were designed and executed appropriately to test their hypothesis. Their data support their conclusion.

Weaknesses:

The nonlinear interocular suppression found in this study, could potentially be partially exaggerated by the nonlinear properties of calcium signals. One of the authors of this study has previously reported that the particular GCaMP used in this study has a nice proportional relationship with firing rate of a neuron. So the concern of exaggeration probably does not apply to this particular study. The concern would apply to others who try similar measurements with other versions of GCaMP.

The implication of their finding is that strong ocular dominance is the result of release from interocular suppression by a monocular stimulus, rather than the lack of binocular combination as many traditional studies have assumed. This could significantly advance our understanding of the binocular combination circuitry of V1. The entire population of neurons could be part of a binocular combination circuitry present in V1.

Reviewer #3 (Public Review):

Summary

The authors have made simultaneous recordings of the responses of large numbers of neurons from the primary visual cortex of macaque monkeys using optical two-photon imaging of calcium signals from the superficial layers of the cortex. Recordings were made to compare the responses of the cortical neurons under normal binocular viewing of a flat screen with both eyes open and monocular viewing of the same screen with one eye's view blocked by a translucent filter. The screen displayed visual stimuli comprising small contrast patches of Gabor function distributions of luminance, a stimulus that is known to excite cortical neurons.

Strengths

This is an important data set, given the large number of neurons recorded. The authors present a simple model to explain binocular combination of neuronal signals from the right and left eyes. The work advances the use of two-photon imaging in the cerebral neocortex. The research design adds valuable information to our understanding of the organization of binocular vision in macaque monkeys, which are the only realistic animal model of human vision for the study of binocular interactions.

Limitations and Weaknesses

(1) Given that these recordings are made optically, these results reflect primarily activations of neurons in the superficial layers of the cortex. This limitation arises from the usual constraints (depth of cortex, degree of myelination) on optical imaging in the macaque cortex. This means that the sample of neurons forming this data set is not fully representative of the population of binocular neurons within the visual cortex. This limitation is important in comparing the outcome of these experiments with the results from other studies of binocular combination, which have used single-electrode recording. Electrode recording will result in a sample of neurons that is drawn from many layers of the cortex, rather than just the superficial layers, noting that electrode recordings also carry different risks of sampling bias.

(2) Single neuron recording of binocular neurons in the primary visual cortex has shown that these neurons often have some spontaneous activity. Assessment of this spontaneous level of firing is important for accurate model fitting [1]. The present imaging approach works exclusively with differential measurements of neuronal signals, so assessment of the level of spontaneous activity is not feasible.

(3) The arrangements for visual stimulation and comparison of binocular and monocular responses mean that the stereoscopic disparity of the binocular stimuli is always at zero or close to zero. The consequence is that the experimental design does not test the cortical response over a range of different binocular depths.

The animal's fixation point is in the centre of a single display that is viewed binocularly. The fixation point is, by definition, at zero disparity.. Provided that the animals accurately converged their eyes on the binocular fixation point, then the disparity of the visual stimuli across the whole display will always be at or close to zero. However, we already know from earlier work that neurons in the visual cortex exhibit a range of selectivity for binocular disparity. Some neurons have their peak response at non-zero disparities, representing binocular depths nearer than the fixation depth or beyond it.

There are also other neurons whose response is maximally suppressed by disparities at the depth of the fixation point (so-called Tuned Inhibitory [TI] neurons). The simple model and analysis presented in the paper for the summation of monocular responses to predict binocular responses will perform adequately for neurons that are tuned to zero disparity, so-called tuned excitatory neurons [TE], but is necessarily compromised when applied to neurons that have other, different tuning profiles for binocular disparity. Specifically, when neurons are stimulated binocularly with a non-preferred disparity, the binocular response may be lower than the monocular response [2, 3]. The same limitation applies to another recent paper [4].

This more realistic view of binocular responses needs to be considered further to gain a full picture of the operation of the visual cortex in responding to binocular depth

Citations

1. Prince, S.J.D., Pointon, A.D., Cumming, B.G., and Parker, A.J., (2002). Quantitative analysis of the responses of V1 neurons to horizontal disparity in dynamic random-dot stereograms. Journal of Neurophysiology, 87: 191-208.

2. Prince, S.J.D., Cumming, B.G., and Parker, A.J., (2002). Range and mechanism of encoding of horizontal disparity in macaque V1. Journal of Neurophysiology, 87: 209-221.

3. Poggio, G.F. and Fischer, B., (1977). Binocular interaction and depth sensitivity in striate and prestriate cortex of behaving rhesus monkey. Journal of Neurophysiology, 40: 1392-1405 doi 10.1152/jn.1977.40.6.1392.

4. B. A. Mitchell, K. Dougherty, J. A. Westerberg, B. M. Carlson, L. Daumail, A. Maier, et al. (2022) Stimulating both eyes with matching stimuli enhances V1 responses.<br /> iScience 2022 Vol. 25 Issue 5 DOI: 10.1016/j.isci.2022.104182

Author Response

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Zeng and Staley provide a valuable analysis of the molecular requirements for the export of a reporter mRNA that contains a lariat structure at its 5' end in the budding yeast S. cerevisiae. The authors provide evidence that this is regulated by the main mRNA export machinery (Yra1, Mex67, Nab2, Npl3, Tom1, and Mlp1). Of note, Mlp1 has been mainly implicated in the nuclear retention of unspliced pre-mRNA (i.e. quality control), and relatively little has been done to investigate its role in mRNA export in budding yeast.

Strengths:

There is relatively little information in the current literature about the nuclear export of splicing intermediates. This paper provides one of the first analyses of this process and dissects the molecular components that promote this form of RNA export. Overall, the strength of the data presented in the manuscript is solid. The paper is well written and the message is clear and of general interest to the mRNA community.

We thank the reviewer for highlighting these strengths.

Weaknesses:

There are three problems with the paper, although these are not major and likely would not affect the final model as most aspects of the molecular details are confirmed by multiple complementary assays.

(1) The brG reporter produces both unspliced pre-mRNA and a lariat-containing intermediate RNA. Based on the primer extension assay the authors claim that only 33% of the final product is in pre-mRNA form and that this "is insufficient to account for the magnitude of the cytoplasmic signal from the brG reporter (83%)". Nevertheless, it is possible that primer extension is incomplete or that the lariat-containing RNA is inaccessible for smFISH. The authors could easily perform a dual smFISH experiment (similar to Adivarahan et l., Molecular Cell 2018) where exon 1 is labelled with probes of one color, and the region that overlaps the lariat-containing intermediate is labelled with probes of a second color. If the authors are correct, then one-third of the smFISH foci should have both labels and the rest would have only the second label. This would also confirm that the latter (i.e. the lariat-containing RNAs) are exported to the cytoplasm. Using this approach, the authors could then show that MLP1-depletion (or depletion of any of the other factors) affect(s) one pool of RNAs (i.e. those that are lariat-containing) but not the other (i.e. pre-mRNA). Including these experiments would make the evidence for their model more convincing.

We appreciate the reviewer’s comments and suggestions. Concerning the primer extension analysis, we are considering alternative assays to quantitate the pre-mRNA and lariat intermediate levels. Concerning the accessibility of the lariat intermediate in smRNA-FISH, in a dbr1∆ strain the only major species from the UAc reporter that is detected by primer extension is the lariat intermediate (Fig. S3), and this reporter is readily detected by smRNA-FISH, indicate that the lariat intermediate is accessible to smRNA-FISH. Concerning discriminating between pre-mRNA and lariat intermediate by smRNA-FISH, we agree with the reviewer that a dual smFISH experiment would directly distinguish between the signals of these species. The brG reporter we used in most smRNA-FISH experiments has a 5’ exon that is too short for smRNA-FISH probes, as is typical of most budding yeast 5’ exons. We have tried to replace the 5’ exon with a longer sequence (GFP) to allow for smRNA-FISH; however, this substitution inhibited splicing. Therefore, to distinguish signals from pre-mRNA versus lariat intermediate, we used additional reporters: G1c and brC reporters, which accumulate pre-mRNA essentially exclusively (Fig. S2A-C), and the UAc reporter, which accumulates lariat intermediate exclusively, in a dbr1∆ strain (Fig. S3). Whereas the mlp1 deletion did not change beta-galactosidase activities of the G1c and brC pre-mRNA-accumulating reporters (Fig. S2E), the mlp1 deletion in a dbr1∆ background did reduce the beta-galactosidase activities of the UAc lariat intermediate-accumulating reporter (Fig. 3D) and did increase smRNA-FISH signal of this reporter in the nucleus (Fig. 3E). These observations corroborate our interpretation based on the brG reporter that Mlp1p is required for efficient export of lariat intermediates but not pre-mRNAs.

(2) In some cases, the number of smFISH foci appears to change drastically depending on the genetic background. This could either be due to the stochastic nature of mRNA expression between cells or reflect real differences between the genetic backgrounds that could alter the interpretation of the other observations.

We thank the reviewer for raising this point. We will review our data to distinguish between these possibilities.

(3) The authors state in the discussion that "the general mRNA export pathway transports discarded lariat intermediates into the cytoplasm". Although this appears to be the case for the reporters that are investigated in this paper, I don't think that the authors should make such a broad sweeping claim. It may be that some discarded lariat intermediates are exported to the cytoplasm while others are targeted for nuclear retention and/or decay.

The reviewer’s point is well-taken. We will revise the wording accordingly.

Reviewer #2 (Public Review):

In this report, Zeng and Staley have used an elegant combination of RNA imaging approaches (single molecule FISH), RNA co-immunoprecipitations, and translation reporters to characterize the factors and pathways involved in the nuclear export of splicing intermediates in budding yeast. Their study notably involves the use of specific reporter genes, which lead to the accumulation of pre-mRNA and lariat species, in a battery of mutants impacting mRNA export and quality control.

The authors convincingly demonstrate that mRNA species expressed from such reporters are exported to the cytoplasm in a manner depending on the canonical mRNA export machinery (Mex67 and its adaptors) and the nuclear pore complex (NPC) basket (Mlp1). Interestingly, they provide evidence that the export of splicing intermediates requires docking and subsequent undocking at the nuclear basket, a step possibly more critical than for regular mRNAs.

We thank the reviewer for this overall positive assessment.

However, their assays do not always allow us to define whether the impacted mRNA species correspond to lariats and/or pre-mRNAs. This is all the more critical since their findings apparently contradict previous reports that supported a role for the nuclear basket in pre-mRNA quality control. These earlier studies, which were similarly based on the use of dedicated yet distinct reporters, had found that the nuclear basket subunit Mlp1, together with different cofactors, prevents the export of unspliced mRNA species. It would be important to clarify experimentally and discuss the possible reasons for these discrepancies.

It is true that we did not assess export of all reporters in all mutant strains by smFISH; however, we did validate the key conclusion that the export of lariat intermediates requires the nuclear basket gene MLP1: the export of both the brG reporter (mostly lariat intermediate) and the UAc reporter (exclusively lariat intermediate) showed a dependence on MLP1 (Fig. 3). Further, by beta-galactosidase activity, we tested in total five separate reporters – three that accumulated lariat intermediate and two that accumulated exclusively pre-mRNA; only the three reporters accumulating lariat intermediate showed a dependence of export on MLP1 (Fig. 4B,D; Fig S2D); the reporters accumulating pre-mRNA did not show a dependence on MLP1 (Fig. S2E), further validating our main conclusion. We are considering additional experiments to validate this key conclusion even further. Also, see response to comment 1 from reviewer 1.

We agree that the main conclusion from this manuscript differs from earlier studies. A key difference is that prior studies monitored exclusively pre-mRNA. In our study, we monitored pre-mRNA and lariat intermediate species and in doing so revealed a role for MLP1 in the export of lariat intermediates. This study, our previous study, as well as the previous studies of others have all provided evidence for efficient export of pre-mRNA; all of these studies are in conflict with the studies purporting a general role for the nuclear basked in retaining immature mRNA. Still, these past apparently conflicting studies can be re-interpreted in the context of our model that the export of such species requires docking at the nuclear basket, followed by undocking. In a revised manuscript, we will discuss the possibility that pre-mRNA apparently “retained” by the nuclear basket are stalled in export at the undocking stage.

Reviewer #3 (Public Review):

Summary:

Zeng and Stanley show that in yeast, intron-lariat intermediates that accumulated due to defects in pre-mRNA splicing, are transported to the cytoplasm using the canonical mRNA export pathway. Moreover, they demonstrate that export requires the nuclear basket, a sub-structure of the nuclear pore complex previously implicated with the retention of immature mRNAs. These observations are important as they put into question a longstanding model that the main role of the nuclear basket is to ensure nuclear retention of immature or faulty mRNAs.

Strengths:

The authors elegantly combine genetic, biochemical, and single-molecule resolution microscopy approaches to identify the cellular pathway that mediates the cytoplasmic accumulation of lariat intermediates. Cytoplasmic accumulation of such splicing intermediates had been observed in various previous studies but how these RNAs reach the cytoplasm had not yet been investigated. By using smFISH, the authors present compelling, and, for the first time, direct evidence that these intermediates accumulate in the cytoplasm and that this requires the canonical mRNA export pathway, including the RNA export receptor Mex67 as well as various RNA-binding proteins including Yra1, Npl3 and Nab2. Moreover, they show that the export of lariat intermediates, but not mRNAs, requires the nuclear basket (Mlp1) and basket-associated proteins previously linked to the mRNP rearrangements at the nuclear pore. This is a surprising and important observation with respect to a possible function of the nuclear basket in mRNA export and quality control, as it challenges a longstanding model that the role of the basket in mRNA export is primarily to act as a gatekeeper to ensure that immature mRNAs are not exported. As discussed by the authors, their finding suggests a role for the basket in promoting the export of certain types of RNAs rather than retention, a model also supported by more recent studies in mammalian cells. Moreover, their findings also collaborate with a recent paper showing that in yeast, not all nuclear pores contain a basket (PMID: 36220102), an observation that also questioned the gatekeeper model of the basket, as it is difficult to imagine how the basket can serve as a gatekeeper if not all nuclear pore contain such a structure.

We thank the reviewer for highlighting the importance and surprising nature of our findings.

Weaknesses:

One weakness of this study is that all their experiments rely on using synthetic splicing reporter containing a lacZ gene that produces a relatively long transcript compared to the average yeast mRNA.

We are considering repeating some of our experiments to monitor export of RNAs with more average lengths.

The rationale for using a reporter containing the brG (G branch point) resulting in more stable lariat intermediates due to them being inefficient substrates for the debranching enzyme Dbr1 could be described earlier in the manuscript, as this otherwise only becomes clear towards the end, what is confusing.

We thank the reviewer for this comment. We will revise the text to explain sooner the rationale for using the brG reporter to assess the export of lariat intermediates.

Discussion of their observation in the context that, in yeast, not all pores contain a basket would be useful.

Thanks for this suggestion. We will raise this point that a nuclear basket is not present on all nuclear pores and discuss the implications.

eLife assessment

This is an important study that demonstrates that RNA intermediates arising from improper splicing are exported out of the nucleus via the canonical mRNA export machinery and the nuclear pore basket. The authors provide convincing evidence that the role of the nuclear basket rather than retaining the transcripts is stimulating their export, putting into question the current model of the role of the basket. The conclusions are in line with recent studies in mammalian cells that suggest that the basket's role in mRNA export and quality control has to be revised.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Zeng and Staley provide a valuable analysis of the molecular requirements for the export of a reporter mRNA that contains a lariat structure at its 5' end in the budding yeast S. cerevisiae. The authors provide evidence that this is regulated by the main mRNA export machinery (Yra1, Mex67, Nab2, Npl3, Tom1, and Mlp1). Of note, Mlp1 has been mainly implicated in the nuclear retention of unspliced pre-mRNA (i.e. quality control), and relatively little has been done to investigate its role in mRNA export in budding yeast.

Strengths:

There is relatively little information in the current literature about the nuclear export of splicing intermediates. This paper provides one of the first analyses of this process and dissects the molecular components that promote this form of RNA export. Overall, the strength of the data presented in the manuscript is solid. The paper is well written and the message is clear and of general interest to the mRNA community.

Weaknesses:

There are three problems with the paper, although these are not major and likely would not affect the final model as most aspects of the molecular details are confirmed by multiple complementary assays.

(1) The brG reporter produces both unspliced pre-mRNA and a lariat-containing intermediate RNA. Based on the primer extension assay the authors claim that only 33% of the final product is in pre-mRNA form and that this "is insufficient to account for the magnitude of the cytoplasmic signal from the brG reporter (83%)". Nevertheless, it is possible that primer extension is incomplete or that the lariat-containing RNA is inaccessible for smFISH. The authors could easily perform a dual smFISH experiment (similar to Adivarahan et l., Molecular Cell 2018) where exon 1 is labelled with probes of one color, and the region that overlaps the lariat-containing intermediate is labelled with probes of a second color. If the authors are correct, then one-third of the smFISH foci should have both labels and the rest would have only the second label. This would also confirm that the latter (i.e. the lariat-containing RNAs) are exported to the cytoplasm. Using this approach, the authors could then show that MLP1-depletion (or depletion of any of the other factors) affect(s) one pool of RNAs (i.e. those that are lariat-containing) but not the other (i.e. pre-mRNA). Including these experiments would make the evidence for their model more convincing.

(2) In some cases, the number of smFISH foci appears to change drastically depending on the genetic background. This could either be due to the stochastic nature of mRNA expression between cells or reflect real differences between the genetic backgrounds that could alter the interpretation of the other observations.

(3) The authors state in the discussion that "the general mRNA export pathway transports discarded lariat intermediates into the cytoplasm". Although this appears to be the case for the reporters that are investigated in this paper, I don't think that the authors should make such a broad sweeping claim. It may be that some discarded lariat intermediates are exported to the cytoplasm while others are targeted for nuclear retention and/or decay.

Reviewer #2 (Public Review):

In this report, Zeng and Staley have used an elegant combination of RNA imaging approaches (single molecule FISH), RNA co-immunoprecipitations, and translation reporters to characterize the factors and pathways involved in the nuclear export of splicing intermediates in budding yeast. Their study notably involves the use of specific reporter genes, which lead to the accumulation of pre-mRNA and lariat species, in a battery of mutants impacting mRNA export and quality control.

The authors convincingly demonstrate that mRNA species expressed from such reporters are exported to the cytoplasm in a manner depending on the canonical mRNA export machinery (Mex67 and its adaptors) and the nuclear pore complex (NPC) basket (Mlp1). Interestingly, they provide evidence that the export of splicing intermediates requires docking and subsequent undocking at the nuclear basket, a step possibly more critical than for regular mRNAs.

However, their assays do not always allow us to define whether the impacted mRNA species correspond to lariats and/or pre-mRNAs. This is all the more critical since their findings apparently contradict previous reports that supported a role for the nuclear basket in pre-mRNA quality control. These earlier studies, which were similarly based on the use of dedicated yet distinct reporters, had found that the nuclear basket subunit Mlp1, together with different cofactors, prevents the export of unspliced mRNA species. It would be important to clarify experimentally and discuss the possible reasons for these discrepancies.

Reviewer #3 (Public Review):

Summary:

Zeng and Stanley show that in yeast, intron-lariat intermediates that accumulated due to defects in pre-mRNA splicing, are transported to the cytoplasm using the canonical mRNA export pathway. Moreover, they demonstrate that export requires the nuclear basket, a sub-structure of the nuclear pore complex previously implicated with the retention of immature mRNAs. These observations are important as they put into question a longstanding model that the main role of the nuclear basket is to ensure nuclear retention of immature or faulty mRNAs.

Strengths:

The authors elegantly combine genetic, biochemical, and single-molecule resolution microscopy approaches to identify the cellular pathway that mediates the cytoplasmic accumulation of lariat intermediates. Cytoplasmic accumulation of such splicing intermediates had been observed in various previous studies but how these RNAs reach the cytoplasm had not yet been investigated. By using smFISH, the authors present compelling, and, for the first time, direct evidence that these intermediates accumulate in the cytoplasm and that this requires the canonical mRNA export pathway, including the RNA export receptor Mex67 as well as various RNA-binding proteins including Yra1, Npl3 and Nab2. Moreover, they show that the export of lariat intermediates, but not mRNAs, requires the nuclear basket (Mlp1) and basket-associated proteins previously linked to the mRNP rearrangements at the nuclear pore. This is a surprising and important observation with respect to a possible function of the nuclear basket in mRNA export and quality control, as it challenges a longstanding model that the role of the basket in mRNA export is primarily to act as a gatekeeper to ensure that immature mRNAs are not exported. As discussed by the authors, their finding suggests a role for the basket in promoting the export of certain types of RNAs rather than retention, a model also supported by more recent studies in mammalian cells. Moreover, their findings also collaborate with a recent paper showing that in yeast, not all nuclear pores contain a basket (PMID: 36220102), an observation that also questioned the gatekeeper model of the basket, as it is difficult to imagine how the basket can serve as a gatekeeper if not all nuclear pore contain such a structure.

Weaknesses:

One weakness of this study is that all their experiments rely on using synthetic splicing reporter containing a lacZ gene that produces a relatively long transcript compared to the average yeast mRNA.

The rationale for using a reporter containing the brG (G branch point) resulting in more stable lariat intermediates due to them being inefficient substrates for the debranching enzyme Dbr1 could be described earlier in the manuscript, as this otherwise only becomes clear towards the end, what is confusing.

Discussion of their observation in the context that, in yeast, not all pores contain a basket would be useful.

Author Response:

Reviewer #1 (Public Review):

Summary:

The authors identified that genetically and pharmacological inhibition of CERS1, an enzyme implicated in ceramides biosynthesis worsen muscle fibrosis and inflammation during aging.<br /> Strengths:

The study points out an interesting issue on excluding CERS1 inhibition as a therapeutic strategy for sarcopenia. Overall, the article it's well written and clear.<br /> Weaknesses:

Many of the experiments confirmed previous published data, which also show a decline of CERS1 in ageing and the generation and characterization of a muscle specific knockout mouse line. The mechanistic insights of how the increased amount of long ceramides (cer c24) and the decreased of shorter ones (cer c18) might influence muscle mass, force production, fibrosis and inflammation in aged mice have not been addressed.

We thank the reviewer for the assessment and would like to point out that Cers1 had not previously been studied in the context of aging. Moreover, our unbiased pathway analyses in human skeletal muscle implicate CERS1 for the first time with myogenic differentiation, which we validate in cell culture systems. To improve mechanistic insights, as suggested by Reviewer #1, we performed more experiments to gain insights how Cers1 derived c18, and Cers2 derived c24 ceramide species affect myogenesis. We recently showed that knocking out Cers2 reduces c24:0/c24:1 and promotes muscle cell maturation (PMID: 37118545, Fig. 6m-r and Supplementary Fig. 5e). This suggests that the very long chain ceramides c24 might indeed be driving the effect we see upon Cers1 inhibition because we observe an accumulation of c24 ceramides upon Cers1 (c18) inhibition (Fig 2B, Fig 3B, Fig 4A, Fig S3E), which is associated with impaired muscle maturation (Fig 4B-C, Fig S3G-I, Fig S4G-I). To study whether impaired muscle cell differentiation upon Cers1 inhibition is dependent on Cers2, we knocked-down Cers1 alone, or in combination with the knockdown of Cers2. Results show that reduced muscle cell maturation mediated by Cers1KD is rescued by the simultaneous knockdown of Cers2 as shown by gene expression analyses and immunohistochemical validation and quantification. Hence, we believe that reducing Cers1 function during aging might lead to an increase in sphingosine levels as has been shown previously (PMID: 31692231). Increased sphingosine triggers cell apoptosis due to its toxicity (PMID: 12531554). Therefore, channeling accumulating sphingosine towards C24 ceramides may avoid toxicity but, as we show in this manuscript, will reduce the myogenic potential in muscle. However, if also C24 production is blocked by Cers2 inhibition, sphingosine is forced towards the production of other, potentially less toxic or myogenesis-impairing ceramides. We added these new data to the revised manuscript as new Fig 5D-E and new Fig S5G-I.

Reviewer #2 (Public Review):

Summary:

The manuscript by Wohlwend et al. investigates the implications of inhibiting ceramide synthase Cers1 on skeletal muscle function during aging. The authors propose a role for Cers1 in muscle myogenesis and aging sarcopenia. Both pharmacological and AAV-driven genetic inhibition of Cers1 in 18month-old mice lead to reduced C18 ceramides in skeletal muscle, exacerbating age-dependent features such as muscle atrophy, fibrosis, and center-nucleated fibers. Similarly, inhibition of the Cers1 orthologue in C. elegans reduces motility and causes alterations in muscle morphology.<br /> Strengths:

The study is well-designed, carefully executed, and provides highly informative and novel findings that are relevant to the field.

Weaknesses:

The following points should be addressed to support the conclusions of the manuscript.

(1) It would be essential to investigate whether P053 treatment of young mice induces age-dependent features besides muscle loss, such as muscle fibrosis or regeneration. This would help determine whether the exacerbation of age-dependent features solely depends on Cers1 inhibition or is associated with other factors related to age- dependent decline in cell function. Additionally, considering the reported role of Cers1 in whole-body adiposity, it is necessary to present data on mice body weight and fat mass in P053treated aged-mice.

We thank the reviewer to suggest that we study Cers1 inhibition in young mice. In fact, a previous study shows that muscle-specific Cers1 knockout in young mice impairs muscle function (PMID: 31692231). Similar to our observation, these authors report reduced muscle fiber size and muscle force. Therefore, we do not believe that our observed effects of Cers1 inhibition in aged mice are specific to aging, although the phenotypic consequences are accentuated in aged mice. As requested by the reviewer, we attached the mice body weights and fat mass (Author response image 1A-B). The reduced fat mass upon P053 treatment is in line with previously reported reductions in fat mass in chow diet or high fat diet fed young mice upon Cers1 inhibition (PMID: 30605666, PMID: 30131496), again suggesting that the effect of Cers1 inhibition might not be specific to aging.

Author response image 1.

(A-B) Body mass (A) and Fat mass as % of body mass (B) were measured in 22mo C57BL/6J mice intraperitoneally injected with DMSO or P053 using EchoMRI (n=7-12 per group). (C-D) Grip strengh measurements in all limbs (C) or only the forelimbs (D) in 24mo C57BL/6J mice intramuscularly injected with AAV9 particles containing scramble, or shRNA targeting Cers1 (n=8 per group). (E-F) Pax7 gene expression in P053 or AAV9 treated mice (n=6-7 per group) (E), or in mouse C2C12 muscle progenitor cells treated with 25nM scramble or Cers1 targeting shRNA (n=8 per group) (F). (G) Proliferation as measured by luciferase intensity in mouse C2C12 muscle muscle cells treated with 25nM scramble or Cers1 targeting shRNA (n=24 per group). Each column represents one biological replicate. (H) Overlayed FACS traces of Annexin-V (BB515, left) and Propidium Iodide (Cy5, right) of mouse C2C12 muscle myotubes treated with 25nM scramble or Cers1 targeting shRNA (n=3 per group). Quantification right: early apoptosis (Annexin+-PI-), late apoptosis (Annexin+-PI+), necrosis (Annexin--PI+), viability (Annexin--PI-). (I) Normalized Cers2 gene expression in mouse C2C12 muscle muscle cells treated with 25nM scramble or Cers1 targeting shRNA (n=6-7 per group). (J-K) Representative mitochondrial respiration traces of digitonin-permeablized mouse C2C12 muscle muscle cells treated DMSO or P053 (J) with quantification of basal, ATP-linked, proton leak respiration as well as spare capacity and maximal capacity linked respiration (n=4 per group). (L) Reactive oxygen production in mitochondria of mouse C2C12 muscle muscle cells treated DMSO or P053. (M) Enriched gene sets related to autophagy and mitophagy in 24mo C57BL/6J mouse muscles intramuscularly injected with AAV9 particles containing scramble, or shRNA targeting Cers1 (left), or intraperitoneally injected with DMSO or P053 (right). Color gradient indicates normalized effect size. Dot size indicates statistical significance (n=6-8 per group). (N) Representative confocal Proteostat® stainings with quantifications of DMSO and P053 treated mouse muscle cells expressing APPSWE (top) and human primary myoblasts isolated from patients with inclusion body myositis (bottom). (O) Stillness duration during a 90 seconds interval in adult day 5 C. elegans treated with DMSO or 100uM P053. (P) Lifespan of C. elegans treated with DMSO or P053. (n=144-147 per group, for method details see main manuscript page 10).

(2) As grip and exercise performance tests evaluate muscle function across several muscles, it is not evident how intramuscular AAV-mediated Cers1 inhibition solely in the gastrocnemius muscle can have a systemic effect or impact different muscles. This point requires clarification.

The grip strength measurements presented in the manuscript come from hindlimb grip strength, as pointed out in the Methods section. We measured grip strength in all four limbs, as well as only fore- (Author response image 1C-D). While forelimb strength did not change, only hindlimb grip strength was significantly different in AAV-Cers1KD compared to the scramble control AAV (Fig 3I), which is in line with the fact that we only injected the AAV in the hindlimbs. This is similar to the effect we observed with our previous data where we saw altered muscle function upon IM AAV delivery in the gastrocnemius (PMID: PMID: 34878822, PMID: 37118545). The gastrocnemius likely has the largest contribution to hindlimb grip strength given its size, and possibly even overall grip strength as suggested by a trend of reduced grip strength in all four limbs (Author response image 1C). We also suspect that the hindlimb muscles have the largest contribution to uphill running as we could also see an effect on running performance. While we carefully injected a minimal amount of AAV into gastrocnemius to avoid leakage, we cannot completely rule out that some AAV might have spread to other muscles. We added this information to the discussion of the manuscript as a potential limitation of the study.

(3) To further substantiate the role of Cers1 in myogenesis, it would be crucial to investigate the consequences of Cers1 inhibition under conditions of muscle damage, such as cardiotoxin treatment or eccentric exercise.<br /> While it would be interesting to study Cers1 in the context of muscle regeneration, and possibly mouse models of muscular dystrophy, we think such work would go beyond the scope of the current manuscript.

(4) It would be informative to determine whether the muscle defects are primarily dependent on the reduction of C18-ceramides or the compensatory increase of C24-ceramides or C24-dihydroceramides.

To improve mechanistic insights, as suggested by Reviewer #2, we performed more experiments to gain insights how Cers1 derived c18, and Cers2 derived c24 ceramide species affect myogenesis. We recently showed that knocking out Cers2 reduces c24:0/c24:1 and promotes muscle cell maturation (PMID: 37118545, Fig. 6m-r and Supplementary Fig. 5e). This suggests that the very long chain ceramides c24 might indeed be driving the effect we see upon Cers1 inhibition because we observe an accumulation of c24 ceramides upon Cers1 (c18) inhibition (Fig 2B, Fig 3B, Fig 4A, Fig S3E), which is associated with impaired muscle maturation (Fig 4B-C, Fig S3G-I, Fig S4G-I). To study whether impaired muscle cell differentiation upon Cers1 inhibition is dependent on Cers2, we knocked-down Cers1 alone, or in combination with the knockdown of Cers2. Results show that reduced muscle cell maturation mediated by Cers1KD is rescued by the simultaneous knockdown of Cers2 as shown by gene expression analyses and immunohistochemical validation and quantification. We added these data to the manuscript as new Fig 5D-E, new Fig S5G-I. These data, together with our previous results showing that Degs1 knockout reduces myogenesis (PMID: 37118545, Fig. 6s-x and Fig. 7) suggest that C24/dhC24 might contribute to the age-related impairments in myogenesis. We added the new results to the revised manuscript.

(5) Previous studies from the research group (PMID 37118545) have shown that inhibiting the de novo sphingolipid pathway by blocking SPLC1-3 with myriocin counteracts muscle loss and that C18-ceramides increase during aging. In light of the current findings, certain issues need clarification and discussion. For instance, how would myriocin treatment, which reduces Cers1 activity because of the upstream inhibition of the pathway, have a positive effect on muscle? Additionally, it is essential to explain the association between the reduction of Cers1 gene expression with aging (Fig. 1B) and the age-dependent increase in C18-ceramides (PMID 37118545).

Blocking the upstream enzyme of the ceramide pathway (SPT1) shuts down the entire pathway that is overactive in aging, and therefore seems beneficial for muscle aging. While most enzymes in the ceramide pathway that we studied so far (SPTLC1, CERS2) revealed muscle benefits in terms of myogenesis, inflammation (PMID: 35089797; PMID: 37118545) and muscle protein aggregation (PMID: 37196064), the CERS1 enzyme shows opposite effects. This is also visible in the direction of CERS1 expression compared to the other enzymes in one of our previous published studies (PMID: 37118545, Fig. 1e and Fig. 1f). In the current study, we show that Cers1 inhibition indeed exacerbates age-related myogenesis and inflammation as opposed to the inhibition of Sptlc1 or Cers2. As the reviewer points out, both C18- and C24-ceramides seem to accumulate upon muscle aging. We think this is due to an overall overactive ceramide biosynthesis pathway. Blocking C18-ceramides via Cers1 inhibition results in the accumulates C24-ceramides and worsens muscle phenotypes (see reply to question #4). On the other hand, blocking C24-ceramides via Cers2 inhibition improves muscle differentiation. These observations together with the finding that Cers1 mediated inhibition of muscle differentiation is dependent on proper Cers2 function (new Fig 5D-E, new Fig S5G-I) points towards C24-ceramides as the main culprit of reduced muscle differentiation. Hence, at least a significant part of the benefits of blocking SPTLC1 might have been related to reducing very long-chain ceramides. We believe that reduced Cers1 expression in skeletal muscle upon aging, observed by us and others (PMID: 31692231), might reflect a compensatory mechanism to make up for an overall overactive ceramide flux in aged muscles. Reducing Cers1 function during aging might lead to an increase in sphingosine levels as has been shown previously (PMID: 31692231). Increased sphingosine triggers cell apoptosis due to its toxicity (PMID: 12531554). Therefore, channeling accumulating sphingosine towards C24 ceramides may avoid toxicity but, as we show in this manuscript, will reduce the myogenic potential in muscle. However, if also C24 production is blocked by Cers2 inhibition (new Fig 5E-D, new Fig S5G-I), sphingosine is forced towards the production of other, potentially less toxic, or myogenesis-impairing ceramides. These data are now added to the revised manuscript (see page 7). Details were added to the discussion of the manuscript (see page 8).

Addressing these points will strengthen the manuscript's conclusions and provide a more comprehensive understanding of the role of Cers1 in skeletal muscle function during aging.

Reviewer #1 (Recommendations For The Authors):

The authors identified that genetical and pharmacological inhibition of CERS1, an enzyme implicated in ceramides biosynthesis worsen muscle fibrosis and inflammation during aging.

Even though many of the experiments only confirmed previous published data (ref 21, 11,37,38), which also show a decline of CERS1 in ageing and the generation and characterization of a muscle specific knockout mouse line, the study points out an interesting issue on excluding CERS1 inhibition as a therapeutic strategy for sarcopenia and opens new questions on understanding how inhibition of SPTLC1 (upstream CERS1) have beneficial effects in healthy aging (ref 15 published by the same authors).

Overall, the article it's well written and clear. However, there is a major weakness. The mechanistic insights of how the increased amount of long ceramides (c24) and the decreased of shorter ones (cer c18) might influence muscle mass, force production, fibrosis and inflammation in aged mice have not been addressed. At the present stage the manuscript is descriptive and confirmatory of CERS1 mediated function in preserving muscle mass. The authors should consider the following points:

Comments:

(1) Muscle data

(a) The effect of CERS1 inhibition on myotube formation must be better characterized. Which step of myogenesis is affected? Is stem cell renewal or MyoD replication/differentiation, or myoblast fusion or an increased cell death the major culprit of the small myotubes? Minor point: Figure S1C: show C14:00 level at 200 h; text of Fig S2A and 1F: MRF4 and Myogenin are not an early gene in myogenesis please correct, Fig S2B and 2C: changes in transcript does not mean changes in protein or myotube differentiation and therefore, authors must test myotube formation and myosin expression.

Cers1 inhibition seems to affect differentiation and myoblast fusion. To test other suggested effects we performed more experiments as delineated. Inhibiting Cers1 systemically with the pharmacological inhibitor of Cers1 (P053) or with intramuscular delivery of AAV expressing a short hairpin RNA (shRNA) against Cers1 in mice did not affect Pax7 transcript levels (Author response image 1E). Moreover, we did also not observe an effect of shRNA targeting Cers1 on Pax7 levels in mouse C2C12 muscle progenitor cells (Author response image 1F). To characterize the effect of Cers1 inhibition on muscle progenitor proliferation/renewal, we used scramble shRNA, or shRNA targeting Cers1 in C2C12 muscle progenitors and measured proliferation using CellTiter-Glo (Promega). Results showed that Cers1KD had no significant effect on cell proliferation (Author response image 1G). Next, we assayed cell death in differentiating C2C12 myotubes deficient in Cers1 using FACS Analysis of Annexin V (left) and propidium iodide (right). We found no difference in early apoptosis, late apoptosis, necrosis, or muscle cell viability, suggesting that cell death can be ruled out to explain smaller myotubes (Author response image 1H). These findings support the notion that the inhibitory effect of Cers1 knockdown on muscle maturation are primarily based on effects on myogenesis rather than on apoptosis. Our data in the manuscript also suggests that Cers1 inhibition affects myoblast fusion, as shown by reduced myonucleation upon Cers1KD (Fig S3H right, Fig S5I).

(b) The phenotype of CESR1 knockdown is milder than 0P53 treated mice (Fig S5D and Figure 3F, 3H are not significant) despite similar changes of Cer18:0, Cer24:0, Cer 24:1 concentration in muscles . Why?

Increases in very long chain ceramides were in fact larger upon P053 administration compared to AAVmediated knockdown. For example, Cer24:0 levels increased by >50% upon P053 administration, compared to 20% by AAV injections. Moreover, dhC24:1 increased by 6.5-fold vs 2.5-fold upon P053 vs AAV treatment, respectively. These differences might not only explain the slightly attenuated phenotypes in the AA- treated mice but also underlines the notion that very long chain ceramides might cause muscle deterioration. We believe inhibiting the enzymatic activity of Cers1 (P053) as compared to degrading Cers1 transcripts is a more efficient strategy to reduce ceramide levels. However, we cannot completely rule out multi-organ, systemic effects of P053 treatment beyond its direct effect on muscle. We added these details in the discussion of the revised manuscript (see page 8 of the revised manuscript).

(c) The authors talk about a possible compensation of CERS2 isoform but they never showed mRNA expression levels or CERS2 protein levels aner treatment. Is CERS2 higher expressed when CERS1 is downregulated in skeletal muscle?

We appreciate the suggestion of the reviewer. We found no change in Cers2 mRNA levels upon Cers1 inhibition in mouse C2C12 myoblasts (Author response image 1I). We would like to point out that mRNA abundance might not be the optimal measurement for enzymes due to enzymatic activities. Therefore, we think metabolite levels are a better proxy of enzymatic activity. It should also be pointed out that “compensation” might not be an accurate description as sphingoid base substrate might simply be more available upon Cers1KD and hence, more substrate might be present for Cers2 to synthesize very long chain ceramides. This “re-routing” has been previously described in the literature and hypothesized to be related to avoid toxic (dh)sphingosine accumulation (PMID: 30131496). Therefore, we changed the wording in the revised manuscript to be more precise.

(d) Force measurement of AAV CERS1 downregulated muscles could be a plus for the study (assay function of contractility)

In the current study we measured grip strength in mice, which had previously been shown to be a good proxy of muscle strength and general health (PMID: 31631989). Indeed, our results of reduced muscle grip strength are in line with previous work that shows reduced contractility in muscles of Cers1 deficient mice (PMID: 31692231).

(e) How are degradation pathways affected by the downregulation of CERS1. Is autophagy/mitophagy affected? How is mTOR and protein synthesis affected? There is a recent paper that showed that CerS1 silencing leads to a reduction in C18:0-Cer content, with a subsequent increase in the activity of the insulin pathway, and an improvement in skeletal muscle glucose uptake. Could be possible that CERS1 downregulation increases mTOR signalling and decreases autophagy pathway? Autophagic flux using colchicine in vivo would be useful to answer this hypothesis

Cers1 in skeletal muscle has indeed been linked to metabolic homeostasis (see PMID: 30605666). In line with their finding in young mice we also find reduced fat mass upon P053 treatment in aged mice (Author response image 1A-B). We also looked into mitochondrial bioenergetics upon blocking Cers1 with P053 treatment using an O2k oxygraphy (Author response image 1J-L). Results show that Cers1 inhibition in mouse muscle cells increases mitochondrial respiration, similar to what has been shown before (PMID: 30131496). However, we also found that reactive oxygen species production in mouse muscle cells is increased upon P053 treatment, suggesting the presence of dysfunctional mitochondria upon inhibiting Cers1 with P053.We next looked into the mitophagy/autophagy degradation pathways suggested by the reviewer and do not find convincing evidence supporting that Cers1 has a major impact on autophagy or mitophagy derived gene sets in mice treated with shRNA against Cers1, or the Cers1 pharmacological inhibitor P053 (Author response image 1M).

We then assessed the effect of Cers1 inhibition on transcripts levels related to the mTORC1/protein synthesis, as suggested by the reviewer. Cers1 knockdown in differentiating mouse muscle cells showed only a weak trend to reduce mTORC1 and its downstream targets (new Fig S4A). In line with this, there was no notable difference in protein synthesis in differentiating, Cers1 deficient mouse C2C12 myoblasts as assessed by L-homopropargylglycine (HPG) amino acid labeling using confocal microscopy (new Fig S4B) or FACS analyses (new Fig S4C). However, Cers1KD increased transcripts related to the myostatin-Foxo1 axis as well as the ubiquitin proteasome system (e.g. atrogin-1, MuRF1) (new Fig S4D), suggesting Cers1 inhibition increases protein degradation. We added these details to the revised manuscript on page 7. We recently implicated the ceramide pathway in regulating muscle protein homeostasis (PMID: 37196064). Therefore, we assessed the effect of Cers1 inhibition with the P053 pharmacological inhibitor on protein folding in muscle cells using the Proteostat dye that intercalates into the cross-beta spine of quaternary protein structures typically found in misfolded and aggregated proteins. Interestingly, inhibiting Cers1 further increased misfolded proteins in C2C12 mouse myoblasts expressing the Swedish mutation in APP and human myoblasts isolated from patients with inclusion body myositis (Author response imageure 1N). These findings suggest that deficient Cers1 might upregulate protein degradation to compensate for the accumulation of misfolded and aggregating proteins, which might contribute to impaired muscle function observed upon Cers1 knockdown. Further studies are needed to disentangle the underlying mechanstics.

(f) The balances of ceramides have been found to play roles in mitophagy and fission with an impact on cell fate and metabolism. Did the authors check how are mitochondria morphology, mitophagy or how dynamics of mitochondria are altered in CERS1 knockdown muscles? (fission and fusion). There is growing evidence relating mitochondrial dysfunction to the contribution of the development of fibrosis and inflammation.

Previously, CERS1 has been studied in the context of metabolism and mitochondria (for reference, please see PMID: 26739815, PMID: 29415895, PMID: 30605666, PMID: 30131496). In summary, these studies demonstrate that C18 ceramide levels are inversely related to insulin sensitivity in muscle and mitochondria, and that Cers1 inhibition improves insulin-stimulated suppression of hepatic glucose production and reduced high-fat diet induced adiposity. Moreover, improved mitochondrial respiration, citrate synthase activity and increased energy expenditure were reported upon Cers1 inhibition. Lack of Cers1 specifically in skeletal muscle was also reported to improve systemic glucose homeostasis. While these studies agree on the effect of Cers1 inhibition on fat loss, results on glucose homeostasis and insulin sensitivity differ depending on whether a pharmacologic or a genetic approach was used to inhibit Cers1. The current manuscript describes the effect of CERS1 on muscle function and myogenesis because these were the most strongly correlated pathways with CERS1 in human skeletal muscle (Fig 1C) and impact of Cers1 on these pathways is poorly studied, particularly in the context of aging. Therefore, we would like to refer to the mentioned studies investigating the effect of CERS1 on mitochondria and metabolism.

(2) C.elegans data:

(a) The authors checked maternal RNAi protocol to knockdown lagr-1 and showed alteration of muscle morphology at day 5. They also give pharmacological exposure of P053 drug at L4 stage. Furthermore, the authors also used a transgenic ortholog lagr-1 to perform the experiments. All of them were consistent showing a reduced movement. It would be important to show rescue of the muscle phenotype by overexpressing CERS1 ortholog in knockdown transgenic animals.

We used RNAi to knockdown the Cers1 orthologue, lagr-1, in C.elegans. Therefore, we do not have transgenic animals. Overexpressing lagr-1 in the RNAi treated animals would also not be possible as the RNA from the overexpression would just get degraded.

(b) The authors showed data about distance of C.elegans. It would be interesting to specify if body bends, reversals and stillness are affected in RNAi and transgenic Knockdown worms.

As suggested, we measured trashing and stillness as suggested by the reviewer and found reduced trashing (new Fig S5B) and a trend towards an increase in stillness (Author response image 1O) in P053 treated worms on day 5 of adulthood, which is the day we observed significant differences in muscle morphology and movement (Fig 4D-E, Fig S5A). These data are now included in the revised manuscript.

(c) Is there an effect on lifespan extension by knocking down CERS1?

We performed two independent lifespan experiments in C.elegans treated with the Cers1 inhibitor P053 and found reduced lifespan in both replicate experiments (for second replicate, see Author response image 1P). We added these data to the revised manuscript as new Fig 4H.

How do the authors explain the beneficial effect of sptlc1 inhibition on healthy aging muscle? Discuss more during the article if there is no possible explanation at the moment.

We believe that blocking the upstream enzyme of the ceramide pathway (SPT1) shuts down the entire pathway that is overactive in aging, and therefore is more beneficial for muscle aging. Our current work suggests that at least a significant part of Sptlc1-KD benefits might stem from blocking very long chain ceramides. While SPTLC1 and CERS2 revealed muscle benefits in terms of myogenesis, inflammation (PMID: 35089797; PMID: 37118545) and muscle protein aggregation (PMID: 37196064), the CERS1 enzyme shows opposite effects, which is also visible in Fig 1e and Fig 1f of PMID: 37118545. In the current study, we show that Cers1 inhibition indeed exacerbates aging defects in myogenesis and inflammation as opposed to the inhibition of Sptlc1 or Cers2. The fact that the effect of Cers1 on inhibiting muscle differentiation is dependent on the clearance of Cers2-derived C24-ceramides suggests that reducing very long chain ceramides might be crucial for healthy muscle aging. We added details to the discussion.

Author Response

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

Public Review:

Summary:

This paper reports how mycobacterial cAMP level is increased under stressful conditions and that the increase is important in the survival of the bacterium in animal hosts.

Strengths:

The authors show that under different stresses the response regulator PhoP represses a phosphodiesterase (PDE) that degrades cAMP specifically. Identification of a PDE specific to cAMP is significant progress in understanding Mtb pathogenesis. An increase in cAMP apparently increases bacterial survival upon infection. On the practical side, the reduction of cAMP by increasing PDE can be a means to attenuate the growth of the bacilli. The results have wider implications since PhoP is implicated in controlling diverse mycobacterial stress responses and many bacterial pathogens modulate host cell cAMP level. The results here are straightforward, internally consistent, and of both theoretical and applied interests.

We thank the reviewers for these extremely encouraging comments.

Weaknesses:

Repression of PDE promoter by binding of phosphorylated PhoP could have been shown at higher precision. The binding is now somewhere along a roughly 500 bp region. Although the regulation of PDE is shown to be by transcriptional repression only, it has been described as a homeostatic mechanism. The latter would have required a demonstration of both repression and activation by negative feedback.

We agree. We have now performed EMSA (Electrophoretic Mobility Shift Assay) experiments and included the data showing DNA binding of PhoP to the upstream regulatory region of rv0805 (rv0805up) as a supplemental figure (see Figure 2-figure supplement 1). The supplemental figure, figure caption, and the relevant results have been adjusted accordingly in the revised manuscript.

Further, as recommended by the reviewer we have now removed the term ‘homeostatic mechanism’ and rephrased it with ‘maintenance of cAMP level’ in the manuscript.

Response to Reviewers’ comments

Reviewer #1:

The authors have used homeostasis inappropriately. Homeostasis usually requires negative feedback (a clear example is the regulation of Lambda prm promoter). Here, there is no feedback from changes in PDE or cAMP level to their synthesis. Homeostasis does not belong to this paper anywhere.

As recommended by the reviewer, we have now removed “homeostasis” from the manuscript and mostly replaced it with “maintenance of cAMP level” in the revised manuscript.

The authors have frequently used adverbs at the beginning of a sentence, such as Notably (l.240, 272, 376), Importantly (l.66, 213), More importantly (l.134), Remarkably (l.264), Interestingly (l.115,301), Intriguingly (l.344), unambiguously (l.347), etc. The use of these words is generally counter-productive. The authors should scan the ms. to eliminate them as far as possible. The sentences would read more clearly and become more impactful.

Following reviewer’s recommendation, we have now eliminated most of the adverbs, mostly used at the beginning of sentences, in the revised manuscript.

Specific comments

(1) L.1: "maintenance of homeostasis" or increasing cAMP level.

As suggested by the reviewer, we have now replaced “maintenance of cAMP homeostasis” with “maintenance of cAMP level”.

(2) L.27: mechanism or reason; varying or various.

As recommended by the reviewer, we have now replaced “mechanism” with “reason” and the word “varying” is deleted while incorporating suggested changes in the abstract.

(3) L.28-29: The logic of connecting PhoP to cAMP doesn't follow well. The logic is much better in l.54, l.112-5 and l.130.

We thank the reviewer for this suggestion. We have now modified the statement within the ‘abstract’ in the revised manuscript (duplicated below):

“cAMP is one of the most widely used second messengers which impacts on a wide range of cellular responses in microbial pathogens including M. tuberculosis. Herein, we hypothesized that intra-mycobacterial cAMP level could be controlled by the phoP locus since the major regulator plays a key role in bacterial response against numerous stress conditions.”

(4) L.30: discovers or reveals (?). Also, in l.101.

As recommended by the reviewer, we have now replaced ‘discovers’ with ‘reveals’ in the Abstract and ‘uncovered’ with ‘revealed’ in the Introduction section of the manuscript.

(5) L.31: Delete "The most - - derived". It is not obvious what most fundamental means here. I suggest: We find that PhoP-dependent ---involves specific binding of the regulator---PDE gene.

As recommended by the reviewer, we have modified the statement (duplicated below): “In keeping with these results, we find specific recruitment of the regulator within the promoter region of rv0805 PDE, and absence of phoP or ectopic expression of rv0805 independently accounts for elevated PDE synthesis leading to depletion of intra-mycobacterial cAMP level.”

(6) L.36: --pathway decreases cAMP level, stress tolerance, and survival of the bacilli.

As recommended by the reviewer, we have now modified the statement (duplicated below): “Thus, genetic manipulation to inactivate PhoP-Rv0805-cAMP pathway decreases cAMP level, stress tolerance, and intracellular survival of the bacilli.

(7) L.41: 'keeps encountering" or encounters?

As suggested by the reviewer, we have replaced ‘keeps encountering’ with ‘encounters’ in the ‘Introduction’ section of the revised manuscript.

(8) L.61: responds, carries.

Our apologies for the embarrassing grammatical mistakes. We have rectified these errors in the revised manuscript.

(9) L.67: you mean burst in synthesis level, not burst of cAMP itself.

To improve clarity, we have now modified the statement in the revised manuscript (duplicated below): “Agarwal and colleagues had shown that burst in synthesis of bacterial cAMP upon infection of macrophages, improved bacterial survival by interfering with host signalling pathways (Agarwal et al., 2009)”

Reference

Agarwal N, Lamichhane G, Gupta R, Nolan S, Bishai WR (2009) Cyclic AMP intoxication of macrophages by a Mycobacterium tuberculosis adenylate cyclase. Nature 460: 98-102

(10) L.77: Change Off to Of.

We are sorry for the inaccuracy. The suggested change has been made to the text.

(11) L.83: Did not discuss "degradation" earlier.

Following reviewer’s recommendation, we have now modified the statement in the revised manuscript (duplicated below).

“Together, these results strongly suggest that a balance between cAMP synthesis by adenylate cyclases and cAMP degradation by phosphodiesterases contributes to rapid adaptive response of mycobacteria in a hostile intracellular environment (Johnson and McDonough, 2018; McDonough and Rodriguez, 2011).”

Reference

Johnson RM, McDonough KA (2018) Cyclic nucleotide signaling in Mycobacterium tuberculosis: an expanding repertoire. Pathog Dis 76 (5)

McDonough KA, Rodriguez A (2011) The myriad roles of cyclic AMP in microbial pathogens: from signal to sword. Nature reviews Microbiology 10: 27-38

(12) L.95: Isn't PhoPR a two-component signal transduction system, the terminology that is more specific than a two-protein regulatory system?

As recommended by the reviewer, we have replaced “two protein regulatory system” with more specific “two-component signal transduction system” in the revised manuscript.

(13) L.124: check-point prevents things from happening. Here the mechanism you found allows growth and survival.

We agree. As recommended by the reviewer, we have now modified the sentence in the revised manuscript (duplicated below).

“Together, the newly identified mechanism of regulation of cAMP level allows intraphagosomal survival and growth program of mycobacteria.”

(14) L.132: why not say directly-"---under normal, and NO and acid stress conditions (Fig. 1A).

As recommended by the reviewer, we have now deleted the first part of the sentence and directly stated that “we compared cAMP levels………. under normal, NO and acidic stress conditions” (duplicated below).

“We compared cAMP levels of WT and phoPR-KO (lacking both phoP and phoR), grown under normal, NO stress and acid stress conditions (Fig. 1A).”

(15) L.134: The complementation is quite variable. Also true in Fig. 2A. If no simple answer, you can say- cAMP values increased in complemented cells, although to a variable extent, for reasons unknown.

We agree with the reviewer. We have now incorporated new text in the ‘Results’ section of the revised manuscript (duplicated below):

“A higher cAMP level in the complemented strain under NO stress is possibly attributable to reproducibly higher phoP expression in the complemented mutant under specific stress conditions (Khan et al., 2022).”

(16) L.154: You rather not say "conclude" and "most likely" at the same time. How about replacing "we conclude" with suggests? In that case, no need to say "most likely". Also, in l.306-7 & l.322-3.

We thank the reviewer for these suggestions. We have now modified the statements in the revised manuscript (duplicated below).

“We suggest that lower cAMP level of the mutant is not due to its higher efficacy of cAMP secretion.”

Following reviewer’s recommendation, we have incorporated similar changes in two other places of the ‘Results’ section of the revised manuscript.

(17) L.161: introduce both the acronyms here and not in l.162.

Following reviewer’s recommendation, we have made the suggested changes.

(18) L.164: Second, (to be in line with First).

We have made the suggested change.

(19). Fig. 2C: There are no black and white bars. This is an important figure because the results appear in the abstract. The signal change from pH 7 to 4.5 is not much. An independent approach would have been desirable. If it were E. coli, I would have suggested beta-gal assay or in vivo footprints. Is a PhoP binding site recognizable in the promoter region of rv0805?

We apologize for the inaccuracy. We have corrected it in the revised manuscript. Also, we have now carried out DNA binding assays, and included the EMSA data of rv0805 upstream regulatory region binding to phosphorylated PhoP (P~PhoP) as a supplemental figure (Figure 2-figure supplement 1A-B). In this figure, we have also incorporated our results on the likely PhoP binding site within rv0805up. The new figure, figure caption and the relevant results have been adjusted accordingly in the revised manuscript.

(20) L.209: ORFs; also delete "of growth" from the sentence.

The suggested changes were made to the text.

(21) L.213: Delete Importantly and change "failed to" to 'did not' (since you did not motivate the expectation earlier, it is better to state the results in an unbiased way).

As recommended by the reviewer, both changes were included in the revised manuscript.

(22) L.217: The requirement of PhoR is a new result - why say "confirm". Change it to indicate. Also, delete "indeed" here and from L.233.

As recommended by the reviewer, both changes were included in the revised manuscript.

(23) L.224: Are the results in Fig 3-S1A under inducing conditions?

The results shown in Fig 3-S1A are not under inducing conditions of expression. For better clarity, we have modified the sentence describing Figure 3-figure supplement 1A (duplicated below).

“rv0805 ORF was cloned within the multicloning site of integrative pSTki (Parikh et al., 2013) between EcoRI and HindIII sites under the control of Pmyc1tetO promoter, and expression of rv0805 under non-inducing condition was verified by determining the mRNA level (Figure 3 - figure supplement 1A).

Reference:

Parikh et al (2013) Development of a new generation of vectors for gene expression, gene replacement, and protein-protein interaction studies in mycobacteria. Applied and environmental microbiology 79: 1718-1729

(24) L.225: ---cAMP level. Add (Fig. 3C) at the end of the next sentence.

As recommended by the reviewer, both the suggested changes were made to the revised text.

(25) L.231: Delete "Most importantly"- you didn't specify what are other less important results.

We agree. We have now deleted “most importantly” from the sentence in the revised text.

(26) L.243 & 254: Change homeostasis to level? Here you are showing mechanisms that can change cAMP level. Homeostasis here would mean how fluctuations in cAMP level are adjusted, usually requiring negative feedback.

As recommended by the reviewer, ‘homeostasis’ was replaced with ‘level’ in both places.

(27) L.256: stress response or stress? Also, in l.272

We are sorry for the inaccuracy. We have corrected these errors in the revised version of the manuscript.

(28) L.259: Change "maintenance of homeostasis" to 'repressing the rv0805 PDE gene'. It is safer to use a fact-based title. In this section, direct measurement of rv0805 mRNA, and/or cAMP levels in different genetic backgrounds seem desirable.

We agree. As recommended by the reviewer, we have modified the title of the ‘Results’ section in the revised manuscript (duplicated below).

“PhoP contributes to mycobacterial stress tolerance and intracellular survival by repressing the rv0805 PDE expression.”

Please note that direct measurements of rv0805 mRNA and cAMP levels are part of Fig. 3 and Figure 3- figure supplement 1A, respectively.

(29) Fig, 4A: White and grey symbols are not easily discriminated without zooming. Use color for phoPR-KO.

We agree. We have now indicated the phoPR-KO in blue in the revised Fig. 4.

(30) L.264: Delete remarkable or explain what is so remarkable. Aren't the results expected- the PDE level would go up in both cases. Direct measurement of PDE /cAMP levels would take the mystery out of the results.

As recommended by the reviewer, we have deleted ‘remarkably’ in the revised text. We have measured cAMP and PDE expression levels of the four strains in Fig. 3 and Figure 3-figure supplement 1.

(31) L.273: --suggesting a role of ---

We have modified this sentence in the revised version of the manuscript (duplicated below).

“A previous study had reported that phoP-deleted mutant strain was more sensitive to Cumene Hydrogen Peroxide (CHP), suggesting a role of PhoP in regulating mycobacterial stress response to oxidative stress (Walters et al., 2006).”

Reference:

Walters et al. (2006) The Mycobacterium tuberculosis PhoPR two-component system regulates genes essential for virulence and complex lipid biosynthesis. Mol Microbiol 60: 312-330

(32) L.275: Delete "transcriptome". CHP sensitivity alone doesn't speak for transcriptome.

As suggested by the reviewer, we have deleted “transcriptome”. Also, please see our response to the previous comment (above).

(33) Fig. 4D and E: % Colocalization in the Merge panels is not much different among the four strains tested (to an untrained eye). Can the results be explained to readers not used to in vivo studies?

As recommended by the reviewer, we have now incorporated new text to explain the in vivo experiment (duplicated below).

“In this assay, WT-H37Rv inhibits phagosome maturation, whereas phagosomes with phoPR-KO mature into phagolysosomes (Anil Kumar et al., 2016).”

Further, for better clarity of the results shown in Fig. 4D, we have (a) increased size of the figure to highlight the difference in the ‘merge’ panel; (b) included “white arrowheads” in the merge panels of Fig. 4D to indicate auramine labeled mycobacteria, which either have inhibited or facilitated trafficking into lysosomes, and finally (c) incorporated method used to calculate percent co-localization in greater details in the ‘Material and Methods’ section of the revised manuscript.

Reference

Anil Kumar et al. (2016) EspR-dependent ESAT-6 secretion of Mycobacterium tuberculosis requires the presence of virulence regulator PhoP. J Biol Chem. 291, 19018-19030

(34) L.275-6: Delete "next" (also in l.347) and "Note that". In this paragraph, I was expecting some explanation on how phoPR-KO and WT-Rv0805 are behaving similarly. Even if the reason is not known, it should be mentioned.

The suggested changes have been made to the text. Also, as recommended by the reviewer, we have included the following text in the revised manuscript (duplicated below):

“Together, these results reveal similar behaviour of phoPR-KO, and WT-Rv0805 by demonstrating a comparably higher susceptibility of these strains to acidic pH and oxidative stress relative to WT bacteria and indicate a link between intra-mycobacterial cAMP level and bacterial stress response. Collectively, these data suggest that at least one of the mechanisms by which PhoP contributes to global stress response is attributable to maintenance of cAMP level.”

(35) L.281: ---WT and indicate a link between cAMP level and stress response in mycobacteria. (No mention of homeostasis).

The suggested change has been made to the revised text. Please see above our response to point # 34.

(36) L.288, 290: No Thus and no clearly.

Both the suggested changes have been made to the text.

(37) L.297: Can you be more direct and state --is due to reduced cAMP level?

As recommended by the reviewer, we have now modified the sentence to make it more direct in the revised manuscript (duplicated below):

“Together, our findings facilitate an integrated view of our results, suggesting that higher susceptibility of WT-Rv0805 to stress conditions, is attributable to its reduced cAMP level.”

(38) L.307: May delete "most likely----homeostasis". cAMP is not discussed here. The same deletion is desired in l.324.

We agree. As recommended by the reviewer, we have now modified the relevant texts in the revised manuscript. These are duplicated below.

“From these results, we suggest that ectopic expression of rv0805 impacts phagosome maturation arguing in favour of a role of PhoP in influencing phagosome-lysosome fusion in macrophages.”

“Thus, we suggest that one of the reasons which accounts for an attenuated phenotype of phoPR-KO in both cellular and animal models is attributable to PhoP-dependent repression of rv0805 PDE activity, which controls mycobacterial cAMP level.”

(39) L.342: cAMP level is regulated remains---

The suggested change has been made to the revised text (duplicated below):

“Although many bacterial pathogens modulate host cell cAMP level as a common strategy, the mechanism of regulation of mycobacterial cAMP level remains unknown.”

(40) L.373: tone down "most fundamental". It is not obvious what is so profound about a stress-response system that depends on PhoP also depends on PhoR. OR justify what is most fundamental about it.

We agree. Following reviewer’s recommendation, we have modified the text in the revised manuscript (duplicated below):

“In keeping with these results, we find that PhoP-dependent rv0805 expression requires PhoR (Figs. 3A-B), the cognate kinase which activates PhoP in a signal-dependent manner (Gupta et al., 2006; Singh et al., 2023).”

References:

Gupta et al. (2006) Transcriptional autoregulation by Mycobacterium tuberculosis PhoP involves recognition of novel direct repeat sequences in the regulatory region of the promoter. FEBS Letters 580, 5328-5338.

Singh et al. (2023) Dual functioning by the PhoR sensor is a key determinant to Mycobacterium tuberculosis virulence. PLoS Genetics 19(12): e1011070.

(41) L.395: delete correspondingly (?)

The suggested change has been made to the text.

(42) L.396: Delete "appear to" and "somewhat". The uncertainty is already implied in "suggest". The evidence that ectopic expression of rv0805 is functionally equivalent to phoP deletion is quite clear in this paper and not saying that clearly is confusing.

We agree with the reviewer. The suggested changes have been made to the revised text (duplicated below):

“Thus, our results suggest that ectopic expression of rv0805 is functionally equivalent to deletion of the phoP locus.”

(43) L.401: --over-expressing bacilli, induction level of rv0805 expression was significantly different in Matange et al and our studies. The next sentence is also very wordy.

We have made changes to the text to address the reviewer’s concern. Also, the next sentence has been rewritten (duplicated below).

“Although both studies were performed with rv0805 over-expressing bacilli, the fact that important differences in the expression of PDEs, in this study (Matange et al., 2013) and in our assays - yielding significantly different levels of rv0805 expression - most likely account for this discrepancy. While we cannot rule out the possibility of cleavage of other cyclic nucleotides by Rv0805 (Keppetipola & Shuman, 2008; Shenoy et al., 2007; Shenoy et al., 2005), consistent with a previous study our results correlate rv0805 expression with intra-mycobacterial cAMP level (Agarwal et al., 2009).”

References:

Matange et al. (2013) Overexpression of the Rv0805 phosphodiesterase elicits a cAMP-independent transcriptional response. Tuberculosis (Edinb) 93: 492-500.

Keppetipola N, Shuman S (2008) A phosphate-binding histidine of binuclear metallophosphodiesterase enzymes is a determinant of 2',3'-cyclic nucleotide phosphodiesterase activity. J Biol Chem 283: 30942-30949

Shenoy et al. (2007) Structural and biochemical analysis of the Rv0805 cyclic nucleotide phosphodiesterase from Mycobacterium tuberculosis. Journal of molecular biology 365: 211-225

Shenoy et al. (2005) The Rv0805 gene from Mycobacterium tuberculosis encodes a 3',5'-cyclic nucleotide phosphodiesterase: biochemical and mutational analysis. Biochemistry 44: 15695-15704

Agarwal N, Lamichhane G, Gupta R, Nolan S, Bishai WR (2009) Cyclic AMP intoxication of macrophages by a Mycobacterium tuberculosis adenylate cyclase. Nature 460: 98-102

(44) L.409: To avoid saying "conclude" and "most likely" at the same time, can you start the sentence thus: 'We infer that Pho-----rv0805 is a---.

We agree. We have made suggested changes to the text. The modified sentence is duplicated below:

“We infer that PhoP-dependent regulation of Rv0805 is a critical regulator of intra-mycobacterial cAMP level.”

(45) L.424. Delete "According to this model". In the preceding sentence, the subject is results, not model. This whole paragraph needs to be rewritten in fewer lines. The shorter the summary statement, the greater would be its impact (less is more here). I would delete the red circles from the figure- it appears that in the repressed state, you are making more products. Replace the circles with an arrow. The legend could be "Increased cAMP level and effective stress response" and "Decreased cAMP---and reduced---.

We thank the reviewer for these suggestions. Following reviewer’s recommendations, we have made numerous changes and rewritten the paragraph in the revised manuscript (duplicated below):

“In summary, upon sensing low acidic pH as a signal PhoR activates PhoP, P~PhoP binds to rv0805 upstream regulatory region and functions as a specific repressor of Rv0805. Therefore, we observed (a) a reproducibly lower level of cAMP in phoPR-KO relative to WT-H37Rv, (b) a significantly reduced expression of rv0805 in WT-H37Rv, grown under acidic pH relative to normal conditions, and (c) comparable cAMP levels in phoPR-KO and WT-Rv0805. This is why the two strains remain ineffective to mount an appropriate stress response, most likely due to their inability to coordinate regulation of gene expression because of dysregulation of intra-mycobacterial cAMP level. However, without uncoupling regulatory control of PhoPR and rv0805 expression, we cannot confirm that dysregulation of cAMP level accounts for virulence attenuation of phoPR-KO. Given the fact that rv0805-depleted M. tuberculosis is growth attenuated in vivo (McDowell et al., 2023), paradoxically ectopic expression of rv0805 leads to dysregulated metabolic adaptation, thereby resulting in reduced stress tolerance and intracellular survival.”

Also, the suggested changes have been incorporated in Fig. 6 and the figure caption.

Reference

McDowell JR, Bai G, Lasek-Nesselquist E, Eisele LE, Wu Y, Hurteau G, Johnson R, Bai Y, Chen Y, Chan J et al (2023) Mycobacterial phosphodiesterase Rv0805 is a virulence determinant and its cyclic nucleotide hydrolytic activity is required for propionate detoxification. Mol Microbiol 119: 401-422

(46) L.458 & 500: ---was used to transform.

Following reviewer’s recommendation, the suggested changes were made to the text in the Materials and Methods section of the revised manuscript.

(47) L.460: --- antibiotics plates.

Both suggested changes were made to the text.

(48) L.466-7: --they were transferred-pH 4.5) and grown for further-

We thank the reviewer for these suggestions. The suggested changes were made to the text.

(49) L.486: ---full-length ORFs of interest were---

The suggested changes were incorporated in the revised manuscript.

(50) L.497: The RNAs were 20 nt long and complementary---

As recommended by the reviewer, we have modified the text in the revised manuscript (duplicated below).

“The RNAs were 20 nt long and complementary to the non-template strand of the target gene.”

Reviewer #2:

(1) Rephrase this sentence in the abstract: “Because growing evidence connects PhoP with varying stress response, we hypothesized that the level of 3’,5’ cAMP, one of the most widely used second messengers, was regulated by the phoP locus, linking numerous stress responses with cAMP production”.

As recommended by the reviewer, we have now rewritten the sentence. The modified text is incorporated in the revised manuscript (duplicated below):

“cAMP is one of the most widely used second messengers, which impacts on a wide range of cellular responses in microbial pathogens including M. tuberculosis. Herein, we hypothesized that intra-mycobacterial cAMP level could be controlled by the phoP locus since the major regulator plays a key role in bacterial responses against numerous stress conditions.”

Also, please see our response to specific comments #1-3 of Reviewer 1.

(2) Line 134: please describe the complementation strain features as it is mentioned for the first time (plasmid, copy number, promoter etc.) in the manuscript. Especially under NO stress what could be the authors' justification regarding the high cAMP concentration in the complementation strain?

As recommended by the reviewer, the details of construction of the complemented strain have been incorporated in the ‘Materials and Methods’ section of the revised manuscript (duplicated below):

“To complement phoPR expression, pSM607 containing a 3.6- kb DNA fragment of M. tuberculosis phoPR including 200-bp phoP promoter region, a hygromycin resistance cassette, attP site and the gene encoding phage L5 integrase, as detailed earlier (Walters et al., 2006) was used to transform phoPR mutant to integrate at the L5 attB site.”

To address the reviewer’s other concern, we have now included the following sentence in the ‘Results’ section of the revised manuscript (duplicated below):

“A higher cAMP level in the complemented strain under NO stress is possibly attributable to reproducibly higher phoP expression in the complemented mutant under specific stress condition (Khan et al., 2022).”

Reference:

Khan et al. (2022) Convergence of two global regulators to coordinate expression of essential virulence determinants of Mycobacterium tuberculosis. eLife 2022, 11:e80965.

(3) In Figure 1C, it is a bit confusing to see the numbers 1,2,3 and 4 and nothing is referred to these numbers in the figure legend so it's better to remove them.

We agree with the reviewer. We have now removed the lane numbers from the figure (Fig. 1C) in the revised manuscript.

(4) Line 852: rephrase it "insignificantly different".

The suggested change has been made to the text. The modified text is incorporated in the manuscript (duplicated below):

“Note that the difference in expression levels of rv0805 between WT and phoPR-KO was significant (p<0.01), whereas the fold difference in mRNA level between WT and the complemented mutant (Compl.) remains nonsignificant (not indicated).”

(5) Line198-200: There are no open/black bars, they all are coloured bars. Correct the same. The significance test should be done for the same gene (suppose rv0805 up) in different pH conditions. Right now, it is not revealing anything and misleading.

We apologize for the inaccuracy. We have now rectified the error. As recommended by the reviewer, Fig. 4C was modified, and the significance tests were carried out between samples involving identical promoter enrichments under different pH conditions. The modified figure, figure legend, and the relevant results have been adjusted accordingly in the revised manuscript.

(6) Line 213: Is there any difference between this complementation strain (phoPR-KO:: phoPphoR with the one used in Figure 1A, 1B, and 2A? If yes, then please describe it.

The same complemented mutant strain, which has been described in the ‘Materials and Methods’ section of the revised manuscript, was used in the experiments described in Fig. 1A, Fig.1B and Fig. 2A.

(7) Line 223: Please mention the copy number and promoter of the vector construct.

As recommended by the reviewer, we have now mentioned the promoter of the vector and incorporated new text with regard to copy number of the expression vector in the revised manuscript (duplicated below).

“Although copy number of episomal vectors with pAl5000 origin of replication (oriM) have been reported to be 3 by Southern hybridization (Ranes et al, 1990), in this case wild-type and mutant Rv0805 proteins were expressed from single-copy chromosomal integrants (Parikh et al., 2013).”

References

Ranes et al., (1990) Functional analysis of pAL5000, a plasmid from Mycobacterium fortuitum: construction of a "mini" mycobacterium-Escherichia coli shuttle vector. J Bacteriol 172: 2793-2797

Parikh et al., (2013) Development of a new generation of vectors for gene expression, gene replacement, and protein-protein interaction studies in mycobacteria. Applied and environmental microbiology 79: 1718-1729

(8) Figure 3 - Figure Supplement 1: not sure why the authors measured mRNA levels of rv1357 and rv2387? These genes were not overexpressed!

The mRNA levels of rv1357 and rv2387 were measured to show that overexpression of either the wild-type or mutant Rv0805 did not influence expression of other PDEs like Rv1357 and Rv2387. We have now mentioned it explicitly in the revised manuscript (duplicated below).

“In contrast, other PDE encoding genes (rv1357 and rv2387), under identical conditions, demonstrate comparable expression levels in WT-H37Rv and rv0805 over-expressing strains.”

(9) Line 234: Wrong interpretation it should be PDE mRNA levels in WT-Rv0805 and WT-Rv0805M.

As recommended by the reviewer, we have now modified the statement to improve clarity (duplicated below).

“The corresponding mRNA levels of PDEs (wild-type and the mutant) are over-expressed approximately 4.5-6 -fold relative to the genomic rv0805 level of WT-H37Rv (Figure 3-figure supplement 1A).”

(10) Line 237: Remove the sentence "Thus, we conclude......identical expression strategy", you have already talked about why phosphodiesterase activity is crucial for cAMP concentration and it is well understood.

Following reviewer’s recommendation, we have now removed the sentence from the revised manuscript.

(11) Figure 3E: Authors should comment on why the cAMP concentration is not significantly changed even though the mRNA level changes are drastic (~90%). How do you correlate that? Is it because of other PDEs?

We agree. As suggested by the reviewer, we have now incorporated new text in the revised manuscript (duplicated below).

“We speculate that effective knocking down of phoP or rv0805 is not truly reflected in the extent of variation of cAMP levels possibly due to the presence of numerous other mycobacterial PDEs.”

(12) Line 505,506: Is it the translation start site or the transcription start site? Because mRNA level changes are reported.

It is the translational start sites, and gene-specific small guide RNAs were designed to inhibit mRNA expression.

(13) Line 292: There is a difference between red and green bars. Authors should do statistical analysis and then comment on whether overexpression of WT and mutant pde are different or similar, to me they are different; also, explain why the WT-Rv0805 strain is different than the phoPR-KO strain in the context of cell wall metabolism.

As recommended by the reviewer, we have now included statistical significance of the data in the revised version, and modified the text accordingly in the manuscript.

Also, we included text explaining why WT-Rv0805 is different compared to phoPR-KO strain in the context of cell wall metabolism (duplicated below).

“Together, these results suggest that both strains expressing wild type or mutant PDEs share a largely similar cell-wall properties and are consistent with (a) a recent study reporting no significant effect of cAMP dysregulation on mycobacterial cell wall structure/permeability (Wong et al., 2023), and (b) role of PhoP in cell wall composition and complex lipid biosynthesis (Walters et al., 2006; Asensio et al., 2006; Goyal et al., 2011).”

References:

Wong et al. (2023) Cyclic AMP is a critical mediator of intrinsic drug resistance and fatty acid metabolism in M. tuberculosis. eLife 2023; 12: e81177

Walters et al. (2006) The Mycobacterium tuberculosis PhoPR two-component system regulates genes essential for virulence and complex lipid biosynthesis. Mol Microbiol 60: 312-330

Asensio et al. (2006) The Virulence-associated Two-component PhoP-PhoR System Controls the Biosynthesis of Polyketide-derived Lipids in Mycobacterium tuberculosis. J Biol Chem 281: 1313-1316.

Goyal et al. (2011) Phosphorylation of PhoP protein plays direct regulatory role in lipid biosynthesis of Mycobacterium tuberculosis. J Biol Chem 286: 45197-45208

(14) Line 299-303: Authors should explain how the colocalization % are calculated. Also, in the figure 4D merge panel please highlight the difference.

As suggested by the reviewer, we have now explained the methodology used to calculate percent colocalization in greater details. Also, we have modified Figure 4D to highlight the difference between samples shown in merge panel. Please see our response to comment # 33 from the Reviewer 1.

(15) General comment: There are multiple instances where writing needs to be improved.

We are sorry for the inaccuracies. We have now done thorough editing of the manuscript and made numerous corrections throughout.

eLife assessment

This important study describes how PhoP regulates cyclic-AMP production in the human pathogen Mycobacterium tuberculosis. The authors provide convincing evidence that PhoP acts as a repressor of the cyclic-AMP-specific phosphodiesterase, Rv0805, which can degrade cyclic-AMP. The work will be of interest to bacteriologists and whilst the revised manuscript has been substantively improved, there are some outstanding points that could improve clarity and presentation.

Reviewer #1 (Public Review):

Summary:

This paper provides a straightforward mechanism of how mycobacterial cAMP level is increased under stressful conditions and shows that the increase is important for the survival of the bacterium in animal hosts. The cAMP level is increased by decreasing the expression of an enzyme that degrades cAMP.

Strengths:

The paper shows that under different stresses the response regulator PhoP represses a phosphodiesterase (PDE) that degrades cAMP specifically. Identification of<br /> PhoP as a regulator of cAMP is significant progress in understanding Mtb pathogenesis, as increase in cAMP apparently increases bacterial survival upon infection. On the practical side, reduction of cAMP by increasing PDE can be a means to attenuate the growth of the bacilli. The results have wider implications since PhoP is implicated in controlling diverse mycobacterial stress responses and many bacterial pathogens modulate host cell cAMP level. The results here are straightforward, internally consistent, and of both theoretical and applied interests. The results also open considerable future work, especially how increases in cAMP level help to increase survival of the pathogen.

Weaknesses:

It is not clear whether PhoP-PDE Rv0805 is the only pathway to regulate cAMP level under stress.

Reviewer #2 (Public Review):

Summary: In the manuscript, the authors have presented new mechanistic details to show how intracellular cAMP levels are maintained linked to the phosphodiesterase enzyme which in turn is controlled by PhoP. Later, they showed the physiological relevance linked to altered cAMP concentrations.

Strengths: Well thought out experiments. The authors carefully planned the experiments well to uncover the molecular aspects of it diligently.

Weaknesses: Some fresh queries were made based on the author's previous responses and hope to get satisfactory answers this time.

Author Response

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

eLife assessment

This important study reports a novel measurement for the chemotactic response to potassium by Escherichia coli. The authors convincingly demonstrate that these bacteria exhibit an attractant response to potassium and connect this to changes in intracellular pH level. However, some experimental results are incomplete, with additional controls/alternate measurements required to support the conclusions. The work will be of interest to those studying bacterial signalling and response to environmental cues.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper shows that E. coli exhibits a chemotactic response to potassium by measuring both the motor response (using a bead assay) and the intracellular signaling response (CheY phosporylation level via FRET) to step changes in potassium concentration. They find increase in potassium concentration induces a considerable attractant response, with an amplitude larger than aspartate, and cells can quickly adapt (but possibly imperfectly). The authors propose that the mechanism for potassium response is through modifying intracellular pH; they find both that potassium modifies pH and other pH modifiers induce similar attractant responses. It is also shown, using Tar- and Tsr-only mutants, that these two chemoreceptors respond to potassium differently. Tsr has a standard attractant response, while Tar has a biphasic response (repellent-like then attractant-like). Finally, the authors use computer simulations to study the swimming response of cells to a periodic potassium signal secreted from a biofilm and find a phase delay that depends on the period of oscillation.

Strengths:

The finding that E. coli can sense and adapt to potassium signals and the connection to intracellular pH is quite interesting and this work should stimulate future experimental and theoretical studies regarding the microscopic mechanisms governing this response. The evidence (from both the bead assay and FRET) that potassium induces an attractant response is convincing, as is the proposed mechanism involving modification of intracellular pH.

Weaknesses:

The authors show that changes in pH impact fluorescent protein brightness and modify the FRET signal; this measurement explains the apparent imprecise adaptation they measured. However, this effect reduces confidence in the quantitative accuracy of the FRET measurements. For example, part of the potassium response curve (Fig. 4B) can be attributed to chemotactic response and part comes from the pH modifying the FRET signal. Measuring the full potassium response curve of the no-receptor mutants as a control would help quantify the true magnitude of the chemotactic response and the adaptation precision to potassium.

Response: We thank the reviewer for the suggestion. We have now measured the full potassium response curve for the no-receptor mutant (HCB1414-pVS88), as shown in Fig. S4. We characterized the pH effects on CFP and YFP channels at different concentrations of KCl, and the relationship between the ratio of the signal post- to pre-KCl addition and the KCl concentration was established for both channels, as shown in Fig. S4C. The pH-corrected signal after KCl addition for strains with receptors was obtained by dividing the original signal after KCl addition by this ratio at the specific KCl concentration. This was done for both CFP and YFP channels. The pH-corrected responses for the Tar-only and Tsr-only strains are represented by red dots in Fig. 5BC. The recalculated response curve and adaptation curve for the wild-type strain are shown in Fig. S5. The same correction was applied to Fig. 3 as well. We also re-performed the simulations using the corrected dose-response curve and replotted Fig. 6, though the simulation results did not change much.

We have now added a subsection “Revised FRET responses by correcting the pH effects on the brightness of eCFP and eYFP” at line 296 in “Results” to describe this.

The measured response may also be impacted by adaptation. For other strong attractant stimuli, the response typically shows a low plateau before it recovers (adapts). However, in the case of Potassium, the FRET signal does not have an obvious plateau following the stimuli. Do the authors have an explanation for that? One possibility is that the cells may have already partially adapted when the response reaches its minimum, which could indicate a different response and/or adaptation dynamics from that of a regular chemo-attractant? In any case, directly measuring the response to potassium in mutants without adaptation enzymes (CheR, CheB) and with the receptors in different methylation levels would shed more light on the problem.

Response: We appreciate the reviewer’s insightful questions. To observe the low plateau before adaptation, a saturating amount of attractant should be added in a stepwise manner. According to the dose-response curve we measured for potassium, a saturating amount of potassium would be close to 100 mM. In fact, there is a small segment of the low plateau in the step response to 30 mM KCl (Fig. 4C or Fig. S5A). To observe more of this low plateau, we could have used a higher concentration of KCl. However, a stimulation higher than 30 mM KCl will induce substantial physiological changes in the cell, resulting in a significant decrease in fluorescence for both channels (Fig. S7). Therefore, the range of KCl concentration that can be reliably applied in FRET measurements is limited.

The half-time of adaptation at 30 mM KCl was measured to be approximately 80 s, demonstrating a faster adaptation than 0.1 mM MeAsp, which induced a similar magnitude of response. Nevertheless, this is still significantly slower than the time required for medium exchange in the flow chamber, which takes less than 10 s to replace 99% of the medium. Thus, the effect on the measured response magnitude due to adaptation should be small (less than 10%).

We thank the reviewer for the suggestion of measuring the response to potassium in mutants without adaptation enzymes (CheR, CheB) and with the receptors in different methylation levels. However, these mutants are typically less sensitive than the wild-type, exhibiting higher values of K0.5 (Sourjik & Berg, PNAS 99:123, 2002), and thus require an even higher KCl concentration to see the low plateau. Consistent with this, we attempted to measure the response to potassium in a cheRcheB mutant (HCB1382-pVS88). As shown in Fig. R1 below, there is no response to up to 30 mM KCl, suggesting that the sensitive region of the mutant is beyond 30 mM KCl.

The relevant text was added at line 413-424.

Author response image 1.

The response of the cheRcheB mutant (HCB1382-pVS88) to different concentrations of KCl. The blue solid line denotes the original signal, while the red dots represent the pH-corrected signal. The vertical purple (green) dashed lines indicate the moment of adding (removing) 0.01 mM, 0.1 mM, 0.3 mM, 1 mM, 3 mM, 10 mM and 30 mM KCl, in chronological order.

There seems to be an inconsistency between the FRET and bead assay measurements, the CW bias shows over-adaptation, while the FRET measurement does not.

Response: We thank the reviewer for pointing this out. We have now demonstrated that the imprecise adaptation shown in the FRET assay primarily resulted from the pH-induced intensity change of the fluorescent proteins. As shown in Fig. S5A&C, the FRET signal also shows over-adaptation, similar to the bead assay, when we recalculated the response by correcting the CFP and YFP channels.

Now we clarified it at line 315.

The small hill coefficient of the potassium response curve and the biphasic response of the Tar-only strain, while both very interesting, require further explanation since these are quite different than responses to more conventional chemoattractants.

Response: We thank the reviewer for pointing this out. We have now recalculated the pH-corrected results for the dose-response curve (Fig. S5) and the biphasic response of the Tar-only strain (Fig. 5C). The new Hill coefficient is 0.880.14 (meanSD), which is close to the response to MeAsp (1.2) (ref. 46). We suspected that this Hill coefficient of slightly less than 1 resulted from the different responses of Tar and Tsr receptors to potassium.

The Tar-only strain exhibits a repellent response to stepwise addition of low concentrations of potassium less than 10 mM, and a biphasic response above (Fig. 5C). This biphasic response might result from additional pH-effects on the activity of intracellular enzymes such as CheRB and CheA, which may have a different timescale and response from the Tar receptor. We have now added the penultimate paragraph in “Discussion” to talk about the response of the Tar-only strain.

Reviewer #2 (Public Review):

Summary:

Zhang et al investigated the biophysical mechanism of potassium-mediated chemotactic behavior in E coli. Previously, it was reported by Humphries et al that the potassium waves from oscillating B subtilis biofilm attract P aeruginosa through chemotactic behavior of motile P aeruginosa cells. It was proposed that K+ waves alter PMF of P aeruginosa. However, the mechanism was this behaviour was not elusive. In this study, Zhang et al demonstrated that motile E coli cells accumulate in regions of high potassium levels. They found that this behavior is likely resulting from the chemotaxis signalling pathway, mediated by an elevation of intracellular pH. Overall, a solid body of evidence is provided to support the claims. However, the impacts of pH on the fluorescence proteins need to be better evaluated. In its current form, the evidence is insufficient to say that the fluoresce intensity ratio results from FRET. It may well be an artefact of pH change. Nevertheless, this is an important piece of work. The text is well written, with a good balance of background information to help the reader follow the questions investigated in this research work.

In my view, the effect of pH on the FRET between CheY-eYFP and CheZ-eCFP is not fully examined. The authors demonstrated in Fig. S3 that CFP intensity itself changes by KCl, likely due to pH. They showed that CFP itself is affected by pH. This result raises a question of whether the FRET data in Fig3-5 could result from the intensity changes of FPs, but not FRET. The measured dynamics may have nothing to do with the interaction between CheY and CheZ. It should be noted that CFP and YFP have different sensitivities to pH. So, the measurement is likely confounded by the change in intracellular pH. Without further experiments to evaluate the effect of pH on CFP and YFP, the data using this FRET pair is inconclusive.

Response: We thank the reviewer for pointing this out. We have now measured the full potassium response curve for the no-receptor mutant (HCB1414-pVS88), as shown in Fig. S4. We characterized the pH effects on CFP and YFP channels at different concentrations of KCl, and the relationship between the ratio of the signal post- to pre-KCl addition and the KCl concentration was established for both channels, as shown in Fig. S4C. The pH-corrected signal after KCl addition for strains with receptors was obtained by dividing the original signal after KCl addition by this ratio at the specific KCl concentration. This was done for both CFP and YFP channels. The pH-corrected responses for the Tar-only and Tsr-only strains are represented by red dots in Fig. 5BC. The recalculated response curve and adaptation curve for the wild-type strain are shown in Fig. S5. The same correction was applied to Fig. 3 as well. We also re-performed the simulations using the corrected dose-response curve and replotted Fig. 6, though the simulation results did not change much.

We have now added a subsection “Revised FRET responses by correcting the pH effects on the brightness of eCFP and eYFP” at line 296 in “Results” to describe this.

The data in Figure 1 is convincing. It would be helpful to include example videos. There is also ambiguity in the method section for this experiment. It states 100mM KCl was flown to the source channel. However, it is not clear if 100 mM KCl was prepared in water or in the potassium-depleted motility buffer. If KCl was prepared with water, there would be a gradient of other chemicals in the buffer, which confound the data.

Response: We apologize for the ambiguity. The KCl solution used in this work was prepared in the potassium-depleted motility buffer. We have now clarified this at both lines 116 and 497. We now provided an example video, Movie S1, with the relevant text added at line 123.

The authors show that the FRET data with both KCl and K2SO4, and concluded that the chemotactic response mainly resulted from potassium ions. However, this was only measured by FRET. It would be more convincing if the motility assay in Fig1 is also performed with K2SO4.

Response: We thank the reviewer for the suggestion. The aim of comparing the responses to KCl and K2SO4 was to determine the role of chloride ions in the response and to prove that the chemotactic response of E. coli to KCl comes primarily from its response to potassium ions. It is more sensitive to compare the responses to KCl and K2SO4 by using the FRET assay. In contrast, the microfluidic motility assay is less sensitive in revealing the difference in the chemotactic responses, making it difficult to determine the potential role of chloride ions.

Methods:

• Please clarify the promotes used for the constitutive expression of FliCsticky and LacI.

Response: The promoters used for the constitutive expression of LacIq and FliCsticky were the Iq promoter and the native promoter of fliC, respectively (ref. 57).

Now these have been clarified at line 471.

• Fluorescence filters and imaging conditions (exposure time, light intensity) are missing.

Response: Thank you for the suggestion. We have now added more descriptions at lines 535-546: The FRET setup was based on a Nikon Ti-E microscope equipped with a 40× 0.60 NA objective. The illumination light was provided by a 130-W mercury lamp, attenuated by a factor of 1024 with neutral density filters, and passed through an excitation bandpass filter (FF02-438/24-25, Semrock) and a dichroic mirror (FF458-Di02-25x36, Semrock). The epifluorescent emission was split into cyan and yellow channels by a second dichroic mirror (FF509-FDi01-25x36, Semrock). The signals in the two channels were then filtered by two emission bandpass filters (FF01-483/32-25 and FF01-542/32-25, Semrock) and collected by two photon-counting photomultipliers (H7421-40, Hamamatsu, Hamamatsu City, Japan), respectively. Signals from the two photomultipliers were recorded at a sampling rate of 1 Hz using a data-acquisition card installed in a computer (USB-1901(G)-1020, ADlink, New Taipei, Taiwan).

• Please clarify if the temperature was controlled in motility assays.

Response: All measurements in our work were performed at 23 ℃. It was clarified at line 496.

• L513. It is not clear how theta was selected. Was theta set to be between 0 and pi? If not, P(theta) can be negative?

Response: The θ was set to be between 0 and π. This has now been added at line 581.

• Typo in L442 (and) and L519 (Koff)

Response: Thank you. Corrected.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) From the motor measurements the authors find that the CW bias over-adapts to a level larger than prestimulus, but this is not seen in the FRET measurements. What causes this inconsistency? Fig. 2D seems to rule out any change in CheY binding to the motor.

Response: We thank the reviewer for pointing this out. We have now demonstrated that the imprecise adaptation shown in the FRET assay primarily resulted from the pH-induced intensity change of the fluorescent proteins. As shown in Fig. S5A&C, the FRET signal also shows over-adaptation, similar to the bead assay, when we recalculated the response by correcting the CFP and YFP channels.

We now clarified it at line 315.

(2) It would be useful to compare the response amplitude for potassium (Fig. 3C) to a large concentration of both MeAsp and serine. This is a fairer comparison since your work shows potassium acts on both Tar and Tsr. Alternatively, testing a much larger concentration (~10^6 micromolar) at which MeAsp also binds to Tsr would also be useful.

Response: We thank the reviewer for pointing this out. We have now recalculated the response to potassium by correcting the pH-induced effects on fluorescence intensity of CFP and YFP. The response to 30 mM KCl was 1.060.10 times as large as that to 100 μM MeAsp. The aim of the comparison between the responses to potassium and MeAsp was to provide an idea of the magnitude of the chemotactic response to potassium. The stimulus of 100 μM MeAsp is already a saturating amount of attractant and induces zero-kinase activity, thus using a higher stimulus (adding serine or a larger concentration of MeAsp) is probably not needed. Moreover, a larger concentration (~10^6 micromolar) of MeAsp would also induce an osmotactic response.

(3) The fitted Hill coefficient (~0.5) to the FRET response curve is quite small and the authors suggest this indicates negative cooperativity. Do they have a proposed mechanism for negative cooperativity? Have similar coefficients been measured for other responses?

Response: We thank the reviewer for pointing this out. We have now recalculated the pH-corrected results for the dose-response curve (Fig. S5). The new Hill coefficient is 0.880.14 (meanSD), which is close to the response to MeAsp (1.2) (ref. 46). We suspect that this Hill coefficient of slightly less than 1 results from the differing responses of Tar and Tsr receptors to potassium.

(3a) The authors state a few times that the response to potassium is "very sensitive", but the low Hill coefficient indicates that the response is not very sensitive (at least compared to aspartate and serine responses).

Response: We apologize for the confusion. We described the response to potassium as “very sensitive” due to the small value of K0.5. This has now been clarified at line 236.

(3b) Since the measurements are performed in wild-type cells the response amplitude following the addition of potassium may be biased if the cell has already partially adapted. This seems to be the case since the FRET time series does not plateau after the addition of the stimulus. The accuracy of the response curve and hill coefficient would be more convincing if the experiment was repeated with a cheR cheB deficient mutant.

Response: We thank the reviewer for raising these questions. To observe the low plateau before adaptation, a saturating amount of attractant should be added in a stepwise manner. According to the dose-response curve we measured for potassium, a saturating amount of potassium would be close to 100 mM. In fact, there is a small segment of the low plateau in the step response to 30 mM KCl (Fig. 4C or Fig. S5A). To observe more of this low plateau, we could have used a higher concentration of KCl. However, a stimulation higher than 30 mM KCl will induce substantial physiological changes in the cell, resulting in a significant decrease in fluorescence for both channels (Fig. S7). Therefore, the range of KCl concentration that can be reliably applied in FRET measurements is limited.

The half-time of adaptation at 30 mM KCl was measured to be approximately 80 s, demonstrating a faster adaptation than 0.1 mM MeAsp, which induced a similar magnitude of response. Nevertheless, this is still significantly slower than the time required for medium exchange in the flow chamber, which takes less than 10 s to replace 99% of the medium. Thus, the effect on the measured response magnitude due to adaptation should be small (less than 10%).

We thank the reviewer for the suggestion of measuring the response to potassium in mutants without adaptation enzymes (CheR, CheB) and with the receptors in different methylation levels. However, these mutants are typically less sensitive than the wild-type, exhibiting higher values of K0.5 (ref. 46), and thus require an even higher KCl concentration to see the low plateau. Consistent with this, we attempted to measure the response to potassium in a cheRcheB mutant (HCB1382-pVS88). As shown in Fig. R1, there is no response to up to 30 mM KCl, suggesting that the sensitive region of the mutant is beyond 30 mM KCl.

The relevant text was added at line 413-424.

(4) The authors show that the measured imprecise adaptation can be (at least partially) attributed to pH impacting the FRET signal by changing eCFP and eYFP brightness.

(4a) Comparing Fig. 5C and D, the chemosensing and pH response time scales look similar. Therefore, does the pH effect bias the measured response amplitude (just as it biases the adapted FRET level)?

Response: We agree with the reviewer that the pH effect on CFP and YFP biases the measured response amplitude. We have now performed the measurement of dose-response curve to potassium for the no-receptor mutant (HCB1414-pVS88), as shown in Fig. S4. The pH effects on CFP and YFP were corrected. The dose-response curve and adaptation curve were recalculated and plotted in Fig. S5.

(4b) It would help to measure a full response curve (at many concentrations) for the no-receptor strain as a control. This would help distinguish, as a function of concentration, how much response can be attributed to pH impacting the FRET signal versus the true chemotactic response.

Response: We thank the reviewer for the suggestion. We have now performed the measurements for the no-receptor strain. The impact of pH on CFP and YFP has been corrected. The pH-corrected results, previously in Fig.3-5, are now presented in Fig. 3, Fig. S5 and Fig. 5, respectively.

(5) The biphasic response of Tar is strange and warrants further discussion. Do the authors have any proposed mechanisms that lead to this behavior? For the 10mM and 30mM KCl measurements there is a repellent response followed by an attractant response for both adding and removing the stimuli, why is this?

Response: We thank the reviewer for pointing this out. The Tar-only strain exhibits a repellent response to stepwise addition of low concentrations of potassium less than 10 mM, and a biphasic response above (Fig. 5C). This biphasic response might result from additional pH-effects on the activity of intracellular enzymes such as CheRB and CheA, which may have a different timescale and response from the Tar receptor. We have now added the penultimate paragraph in “Discussion” to talk about the response of the Tar-only strain.

(5a) The fact that Tar and Tsr are both attractant (after the initial repellant response in Tar) appears to be inconsistent with previous work on pH response (Ref 52, Yang and Sourjik Molecular Microbiology (2012) 86(6), 1482-1489). This study also didn't see any biphasic response.

Response: We thank the reviewer for pointing this out. The Tar-only strain shows a repellent response to stepwise addition of low concentrations of potassium, specifically less than 10 mM. This is consistent with previous observations of the response of Tar to changes in intracellular pH (refs. 44,45) and also with the work of Yang and Sourjik (new ref. 53), although the work in ref. 53 dealt with the response to external pH change, and bacteria were known to maintain a relatively stable intracellular pH when external pH changes (Chen & Berg, Biophysical Journal (2000) 78:2280-2284). Interestingly, the Tar-only strain exhibits a biphasic response to high potassium concentrations of 10 mM and above. This biphasic response might result from additional pH-effects on the activity of intracellular enzymes such as CheRB and CheA (ref. 56), which may have a different timescale and response from the Tar receptor. We have now added the penultimate paragraph in “Discussion” to talk about the response of the Tar-only strain.

(5b) The response of Tar to the removal of sodium benzoate (Fig. S2) seems to be triphasic, is there any explanation for this?

Response: We thank the reviewer for pointing this out. We have now acknowledged in the legend of Fig. S2 that this response is interesting and warrants further exploration: “The response to the removal of sodium benzoate seems to be a superposition of an attractant and a repellent response, the reason for which deserves to be further explored.”

(6) Fitting the MWC model leads to N=0.35<1. It is fine to use this as a phenomenological parameter, but can the authors comment on what might be causing such a small effective cluster size for potassium response?

Response: We thank the reviewer for pointing this out. We have now recalculated the pH-corrected results for the dose-response curve (Fig. S5). The new Hill coefficient is 0.880.14 (meanSD), which is close to the response to MeAsp (1.2) (ref. 46). We now refit the MWC model to the pH-corrected dose-response curve, obtaining N of 0.85. We think the small N is due partly to the fact that we are fitting the curve with four parameters: N, Kon, Koff, and fm, while only three features of the sigmoid does-response curve are relevant (the vertical scale, the midpoint concentration, and the slope of the sigmoid). Future experiments may determine these parameters more accurately, but they should not significantly affect the simulation results as long as the wild-type dose-response curve is accurate.

(7) The results of the modeling are closely related to Zhu et. al. Phys. Rev. Lett. 108, 128101. Is the lag time for large T related to the adaptation time?

Response: We thank the reviewer for pointing this out. We used a similar framework of modeling as Zhu et. al. The potassium response was also analogous to the chemotactic response to MeAsp. Thus, the results are closely related to Zhu et al. We have now cited Zhu et al. (Ref. 52) and noted this at line 366.

The lag time for large T is related to the adaptation time. We have now simulated the chemotaxis to potassium for large T with different adaptation time by varying the methylation rate kR. The results are shown in Fig. S8. The simulated lag time decreases with the methylation rate kR, but levels off at high values of kR. Now this has been added at line 603.

Minor issues:

• Fig. 1C: should the axis label be y?

Response: Yes, thank you. Now corrected.

• Line 519: Koff given twice, the second should be Kon.

Response: Thank you. Corrected.

• When fitting the MWC model (Eq. 3 and Fig. 6B) did you fix a particular value for m?

Response: m was treated as a fitting parameter, grouped in the parameter fm.

Reviewer #2 (Recommendations For The Authors):

Minor points: - I suggest explaining the acronyms when they first appear in the text (eg CMC, CW, CCW).

Response: Thank you. Now they have been added.

• L144. L242. "decrease" is ambiguous since membrane potential is negative. I understand the authors meant less negative (which is an increase). I suggest to avoid this expression.

Response: Thank you for the suggestion. Now they have been replaced by “The absolute value of the transmembrane electrical potential will decrease”.

• For Fig 1b - it says the shaded area is SEM in the text, but SD in the legend. Please clarify.

Response: Thank you. The annotation in the legend has now been revised as SEM.

• Fig 1C label of x axis should be "y" instead of "x" to be consistent with Fig 1A.

Response: Thank you. It has now been revised.

• In Figure 2, the number of independent experiments as well as the number of samples should be included.

Response: Thank you. The response in Fig. 2C is the average of 83 motors from 5 samples for wild-type strain (JY26-pKAF131). The response in Fig. 2D is the average of 22 motors from 4 samples for the chemotaxis-defective strain (HCB901-pBES38). They have now been added to the legend.

• Regarding the attractant or repelling action of potassium and sucrose, it would be important to have a move showing the cells' behaviours.

Response: We thank the reviewer for the suggestion. We have now provided Movie S1 to show the cells’ behavior to potassium. As shown in Fig. 3B, the chemotactic response to 60 mM sucrose is very small compared to the response to 30 mM KCl. This implies that a noticeable response to sucrose necessitates higher concentrations of stimulation. However, Jerko et al. [Rosko, J., Martinez, V. A., Poon, W. C. K. & Pilizota, T. Proc. Natl Acad. Sci. USA 114, E7969-E7976 (2017).] have shown that high concentrations of sucrose lead to a significant reduction in the speed of the flagella motor. Thus, in a motility assay for sucrose, the osmolarity-induced motility effect may overwhelm the minor repellent-like response.

eLife assessment

In this important study, the authors report a novel measurement of the Escherichia coli chemotactic response and demonstrate that these bacteria display an attractant response to potassium, which is connected to intracellular pH level. Whilst the experiments are mostly convincing, there are some confounders regards pH changes and fluorescent proteins that remain to be addressed.

Reviewer #1 (Public Review):

Summary:

This paper shows that E. coli exhibits a chemotactic response to potassium by measuring both the motor response (using a bead assay) and the intracellular signaling response (CheY phosporylation level via FRET) to step changes in potassium concentration. They find increase in potassium concentration induces a considerable attractant response, with amplitude comparable to aspartate, and cells can quickly adapt (and generally over-adapt). The authors propose that the mechanism for potassium response is through modifying intracellular pH; they find both that potassium modifies pH and other pH modifiers induce similar attractant responses. It is also shown, using Tar- and Tsr-only mutants, that these two chemoreceptors respond to potassium differently. Tsr has a standard attractant response, while Tar has a biphasic response (repellent-like then attractant-like). Finally, the authors use computer simulations to study the swimming response of cells to a periodic potassium signal secreted from a biofilm and find a phase delay that depends on the period of oscillation.

Strengths:

The finding that E. coli can sense and adapt to potassium signals and the connection to intracellular pH is quite interesting and this work should stimulate future experimental and theoretical studies regarding the microscopic mechanisms governing this response. The evidence (from both the bead assay and FRET) that potassium induces an attractant response is convincing, as is the proposed mechanism involving modification of intracellular pH. The updated manuscript controls for the impact of pH on the fluorescent protein brightness that can bias the measured FRET signal. After correction the response amplitude and sharpness (hill coefficient) are comparable to conventional chemoattractants (e.g. aspartate), indicating the general mechanisms underlying the response may be similar. The authors suggest that the biphasic response of Tar mutants may be due to pH influencing the activity of other enzymes (CheA, CheR or CheB), which will be an interesting direction for future study.

Weaknesses:

The measured response may be biased by adaptation, especially for weak potassium signals. For other attractant stimuli, the response typically shows a low plateau before it recovers (adapts). In the case of potassium, the FRET signal does not have an obvious plateau following the stimuli of small potassium concentrations, perhaps due to the faster adaptation compared to other chemoattractants. It is possible cells have already partially adapted when the response reaches its minimum, so the measured response may be a slight underestimate of the true response. Mutants without adaptation enzymes appear to be sensitive to potassium only at much larger concentrations, where the pH significantly disrupts the FRET signal; more accurate measurements would require development of new mutants and/or measurement techniques.

Reviewer #2 (Public Review):

Zhang et al investigated the biophysical mechanism of potassium-mediated chemotactic behavior in E coli. Previously, it was reported by Humphries et al that the potassium waves from oscillating B subtilis biofilm attract P aeruginosa through chemotactic behavior of motile P aeruginosa cells. It was proposed that K+ waves alter PMF of P aeruginosa. However, the mechanism was this behaviour was not elusive. In this study, Zhang et al demonstrated that motile E coli cells accumulate in regions of high potassium levels. They found that this behavior is likely resulting from the chemotaxis signalling pathway, mediated by an elevation of intracellular pH. Overall, a solid body of evidence is provided to support the claims. However, the impacts of pH on the fluorescence proteins need to be better evaluated. In its current form, the evidence is insufficient to say that the fluoresce intensity ratio results from FRET. It may well be an artefact of pH change.

The authors now carefully evaluated the impact of pH on their FRET sensor by examining the YFP and CFP fluorescence with no-receptor mutant. The authors used this data to correct the impact of pH on their FRET sensor. This is an improvement, but the mathematical operation of this correction needs clarification. This is particularly important because, looking at the data, it is not fully convincing if the correction was done properly. For instance, 3mM KCl gives 0.98 FRET signal both in Fig3 and FigS4, but there is almost no difference between blue and red lines in Fig 3. FigS4 is very informative, but it does not address the concern raised by both reviewers that FRET reporter may not be a reliable tool here due to pH change.

The authors show the FRET data with both KCl and K2SO4, concluding that the chemotactic response mainly resulted from potassium ions. However, this was only measured by FRET. It would be more convincing if the motility assay in Fig1 is also performed with K2SO4. The authors did not address this point. In light of complications associated with the use of the FRET sensor, this experiment is more important.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Weaknesses:

The weaknesses are the brevity of the simulations, the concomitant lack of scope of the simulations, the lack of depth in the analysis, and the incomplete relation to other relevant work.

A 1 µs simulation of CCh (Video 1, part 2) shows that m3 (ACHA) is stable, throughout. The DG comparisons, in silico versus in vitro, indicate that 200 ns simulations are sufficient to identify LA versus HA conformational populations. Figure 6-table supplement 1 shows distances. New citations have been added.

Reviewer #2 (Public Review):

Weaknesses:

After carrying out all-atom molecular dynamics, the authors revert to a model of binding using continuum Poisson-Boltzmann, surface area, and vibrational entropy. The motivations for and limitations associated with this approximate model for the thermodynamics of binding, rather than using modern atomistic MD free energy methods (that would fully incorporate configurational sampling of the protein, ligand, and solvent) could be provided. Despite this, the authors report a correlation between their free energy estimates and those inferred from the experiment. This did, however, reveal shortcomings for two of the agonists. The authors mention their trouble getting correlation to experiment for Ebt and Ebx and refer to up to 130% errors in free energy. But this is far worse than a simple proportional error, because -24 Vs -10 kcal/mol is a massive overestimation of free energy, as would be evident if the authors were to instead express results in terms of KD values (which would have an error exceeding a billion fold). The MD analysis could be improved with better measures of convergence, as well as a more careful discussion of free energy maps as a function of identified principal components, as described below. Overall, however, the study has provided useful observations and interpretations of agonist binding that will help understand pentameric ligand-gated ion channel activation.

The objective of the calculations was to identify structural populations, not to estimate binding free energies. We knew the actual LA and HA energies (for all 4 agonists) from real-world electrophysiology experiments. We conclude that the simple PBSA method worked as a tool for identification because the calculated efficiencies match those from experiments (Figure 4B, Figure 4-Source Data 1). We discuss the mismatches in absolute G in the Results and Discussion. Methods for estimating experimental binding free energies are described in a cited, eLife companion paper. The G ratio relates to agonist efficiency.

Main points:

Regarding the choice of model, some further justification of the reduced 2 subunit ECD-only model could be given. On page 5 the authors argue that, because binding free energies are independent of energy changes outside the binding pocket, they could remove the TMD and study only an ECD subunit dimer. While the assumption of distant interactions being small seems somewhat reasonable, provided conformational changes are limited and localised, how do we know the packing of TMD onto the ECD does not alter the ability of the alpha-delta interface to rearrange during weak or strong binding? They further write that "fluctuations observed at the base of the ECD were anticipated because the TMD that offers stability here was absent.". As the TMD-ECD interface is the "gating interface" that is reshaped by agonist binding, surely the TMD-ECD interface structure must affect binding. It seems a little dangerous to completely separate the agonist binding and gating infrastructure, based on some assumption of independence. Given the model was only the alpha and delta subunits and not the pentamer with TMD, I am surprised such a model was stable without some heavy restraints. The authors state that "as a further control we carried out MD simulation of a pentamer docked with ACh and found similar structural changes at the binding pocket compared to the dimer." Is this sufficient proof of the accuracy of the simplified model? How similar was the model itself with and without agonist in terms of overall RMSD and RMSD for the subunit interface and the agonist binding site, as well as the free energy of binding to each model to compare?

The statement that distant interactions are small is not an "assumption", but rather a conclusion based on data. Mutant cycle analysis of 83 pairs shows (with a few exceptions) non-additivity of free energy change prevails only with separations <~15 A (Fig.3 in Gupta et al 2017). Regardless, the adequacy of dimers and convergence by 200 ns are supported by the calculated and experimental agonist efficiencies match (Figure 4B) and the 1 ms simulation (Video 1 part 2). Apo 200ns simulation of the ECD dimer is now added (Figure 2-figure supplement 2) and the dimer interface seems to be adequate (stable).

Although the authors repeatedly state that they have good convergence with their MD, I believe the analysis could be improved to convince us. On page 8 the authors write that the RMSD of the system converged in under 200 ns of MD. However, I note that the graph is of the entire ECD dimer, not a measure for the local binding site region. An additional RMSD of local binding site would be much more telling. You could have a structural isomerisation in the site and not even notice it in the existing graph. On page 9 the authors write that the RMSF in Figure S2 showed instability mainly in loops C and F around the pocket. Given this flexibility at the alpha-delta interface, this is why collecting those regions into one group for the calculation of RMSD convergence analysis would have been useful. They then state "the final MD configuration (with CCh) was well-aligned with the CCh-bound cryo-EM desensitized structure (7QL6)... further demonstrating that the simulation had converged." That may suggest a change occurred that is in common with the global minimum seen in cryo EM, which is good, but does not prove the MD has "converged". I would also rename Figure S3 accordingly.

The description is now changed to “aligns well” with desensitized structure (7QL6.PDB)”. RMSD of not just the binding pocket but the whole ECD dimer is well aligned with first apo (m1) and with desensitized state (m3).

The authors draw conclusions about the dominant states and pathways from their PCA component free energy projections that need clarification. It is important first to show data to demonstrate that the two PCA components chosen were dominant and accounted for most of the variance. Then when mapping free energy as a function of those two PCA components, to prove that those maps have sufficient convergence to be able to interpret them. Moreover, if the free energies themselves cannot be used to measure state stability (as seems to be the case), that the limitations are carefully explained. First, was PCA done on all MD trajectories combined to find a common PC1 & PC2, or were they done separately on each simulation? If so, how similar are they? The authors write "the first two principal components (PC-1 and PC-2) that capture the most pronounced C. displacements". How much of the total variance did these two components capture? The authors write the changes mostly concern loop C and loop F, but which data proves this? e.g. A plot of PC1 and PC2 over residue number might help.

The PCA analyses have been enriched. Figure 3-Source Data 1. shows the dominance of PC1 and PC2. Because the binding energy match was sufficient to identify affinity states, we did not explore additional PCs. Residue-wise PC1 and PC2 analysis and comparison with RMSF are in Figure 2-figure supplement 2. PC1 and PC2 both correlate with fluctuations in loops C and F. Overlap analysis in different runs is shown in Figure 3-figure supplement 1. Lower variance in a particular region of the PCA landscape indicates that the system frequently visits these states, suggesting stability (a preference for these conformations).

The authors map the -kTln rho as a free energy for each simulation as a function of PC1 & PC2. It is important to reveal how well that PC1-2 space was sampled, and how those maps converged over time. The shapes of the maps and the relative depths of the wells look very different for each agonist. If the maps were sampled well and converged, the free energies themselves would tell us the stabilities of each state. Instead, the authors do not even mention this and instead talk about "variance" being the indicator of stability, stating that m3 is most stable in all cases. While I can believe 200ns could not converge a PC1-2 map and that meaningful delta G values might not be obtained from them, the issue of lack of sampling must be dealt with. On page 12 they write "Although the bottom of the well for 3 energy minima from PCA represent the most stable overall conformation of the protein, they do not convey direct information regarding agonist stability or orientation". The reasons why not must be explained; as they should do just that if the two order parameters PC1 and PC2 captured the slowest degrees of freedom for binding and sampling was sufficient. The authors write that "For all agonists and trajectories, m3 had the least variance (was most stable), again supporting convergence by 200 ns." Again the issue of actual free energy values in the maps needs to be dealt with. The probabilities expressed as -kTln rho in kcal/mol might suggest that m2 is the most stable. Instead, the authors base stability only on variance (I guess breadth of the well?), where m3 may be more localised in the chosen PC space, despite apparently having less preference during the MD (not the lowest free energy in the maps).

The motivations and justifications for the use of approximate PBSA energetics instead of atomistic MD free energies should be dealt with in the manuscript, with limitations more clearly discussed. Rather than using modern all-atom MD free energy methods for relative or absolute binding free energies, the author selects clusters from their identified states and does Poisson-Boltzmann estimates (electrostatic, vdW, surface area, vibrational entropy). I do believe the following sentence does not begin to deal with the limitations of that method: "there are limitations with regard to MM-PBSA accurately predicting absolute binding free energies (Genheden & Ryde, 2015; Hou et al., 2011) that depends on the parameterization of the ligand (Oostenbrink et al., 2004)." What are the assumptions and limitations in taking continuum electrostatics (presumably with parameters for dielectric constants and their assignments to regions after discarding solvent), surface area (with its assumptions and limitations), and of course assuming vibration of a normal mode can capture entropy. On page 30, regarding their vibrational entropy estimate, they write that the "entropy term provides insights into the disorder within the system, as well as how this disorder changes during the binding process". It is important that the extent of disorder captured by the vibrational estimate be discussed, as it is not obvious that it has captured entropy involving multiple minima on the system's true 3N-dimensional energy surface, and especially the contribution from solvent disorder in bound Vs dissociated states.

As discussed above, errors in the free energy estimates need to be more faithfully represented, as fractional errors are not meaningful. On page 21 the authors write "The match improved when free energy ratios rather than absolute values were compared." But a ratio of free energies is not a typical or expected measure of error in delta G. They also write "For ACh and CCh, there is good agreement between.Gm1 and GLA and between.Gm3 and GHA. For these agonists, in silico values overestimated experimental ones only by ~8% and ~25%. The agreement was not as good for the other 2 agonists, as calculated values overestimated experimental ones by ~45%(Ebt) and ~130% (Ebt). However, the fractional overestimation was approximately the same for GLA and GHA." See the above comment on how this may misrepresent the error. On page 21 they write, in relation to their large fractional errors, that they "do not know the origin of this factor but speculate that it could be caused by errors in ligand parameterization". However the estimates from the PBSA approach are, by design, only approximate. Both errors in parameterisation (and their likely origin) and the approximate model used, need discussion.

Again, the goal of calculating binding free energy was to identify structural correspondence to LA and HA and not to obtain absolute binding free energy values. Along with the least variance (distribution) for the principle component for m3, it also had the highest binding free energy. An association of m1 to LA and m3 to HA was done after comparing them to experimental values (efficiencies). This comparison not only validates our approach but also underscores the utility of PBSA in supplementing MD and PCA analyses with broader energetics perspectives.

Reviewer #3 (Public Review):

Weaknesses:

Although the match in simulated vs experimental energies for two ligands was very good, the calculated energies for two other ligands were significantly different than the experiment. It is unclear to what extent the choice of method for the energy calculations influenced the results. See above.

A control simulation, such as for an apo site, is lacking. Figure 2-figure supplement 2. shows the results of 200 ns MD simulations of the apo structure (n=2).

Reviewer #4 (Public Review):

Weaknesses:

Timescales (200 ns) do not capture global rearrangements of the extracellular domain, let alone gating transitions of the channel pore, though this work may provide a launching point for more extended simulations. A more general concern is the reproducibility of the simulations, and how representative states are defined. It is not clear whether replicates were included in principal component analysis or subsequent binding energy calculations, nor how simulation intervals were associated with specific states.

We are interested eventually in using MD to study the full isomerization, but these investigations are for the future and likely will involve full length pentamers and longer timescales. However, in response to this query we have in the Discussion raised this issue and offer speculations. See above, PCA has be compared between replicates (Figure 3-figure supplement 1).

Structural analysis largely focuses on snapshots, with limited direct evidence of consistency across replicates or clusters. Figure legends and tables could be clarified.

Snapshots and distance measurements (Figure 6-table supplement 1) were extracted from m1, m2 and m3 plateau regions of trajectories. Incorporated in the legend.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This study gives interesting insights into the possible dynamics of ligand binding in ACh receptors and establishes some prerequisites for necessary and urgent further work. The broad interest in this receptor class means this work will have some reach.

Suggestions:

(1) I found the citation of relevant literature to be rather limited. In the following paper, the agonist glutamate was shown to bind in two different orientations, and also to convert. These are much longer simulations than what is presented here (nearly 50 µs), which allowed a richer view of conformational changes and ligand binding dynamics in the AMPA Receptor. Albert Lau has published similar work on NMDA, delta, and kainate receptors, including some of it in eLife. Perhaps the authors could draw some helpful comparisons with this work.

Yu A et al. (2018) Neurotransmitter Funneling Optimizes Glutamate Receptor Kinetics. Neuron

Likewise, the comparison to a similar piece of work on glycine receptors (not cited, https://pubs.acs.org/doi/10.1021/bi500815f) could be instructive. Several similar computational techniques were used, and interactions observed (in the simulations) between the agonist and the receptor were tested in the context of wet experiments. In the absence of an equivalent process in this paper (no findings were tested using an orthogonal approach, only compared against known results, from perhaps a narrow spectrum of papers), we have to view the major findings of the paper (docking in cis that leads to a ligand somersault) with some hesitancy.

The Gharpure 2019 paper is cited in the context of the delta subunit but this paper was about a3b4 neuronal nicotinic receptors. This could be tidied up. Also, the simulations from that paper could be used as an index of the stability of the HA state (if ligand orientation is being cited as transferrable, other observations could be too).

New citations have been added. It is difficult to generalize from Yu A and Yu R eta al, because in neither study was the ligand orientation associated with LA versus HA binding energy.

(2) "To start, we associated the agonist orientation in the hold end states as cis in AC-LA versus trans in AC-HA."

I think this a valid start, but one is left with the feeling that this is all we have and the validity of the starting state is not tested. What was really shown here? Is the docking reliable? What evidence can the authors summon for the ligand orientation that they use as a starting structure? In addition to docking energies, the match between PBSA and electrophysiology Gs and temporal sequence (m1-m2-m3) support the assignment.

Given that these simulations cover a circumscribed part of the binding process, I think the limitations should be acknowledged. Indeed the authors do mention a number of remaining open questions.

Paragraphs regarding 'catch' have been added to the Discussion.

(3) Results around line 90. Hypothetical structures and states that were determined from Markov analyses are discussed as if they are well understood and identified. Plausible though these are, I think the text should underline at least the source of such information. In these simulations, a further intermediate has been identified.

The model in Figure 1B was first published in 2012 and has been used and extended over the intervening years. In our lab, catch-and-hold is standard. We have published many papers (in top journals), plus reviews, regarding this scheme. We made presentations that are on Youtube. Here, at the end of the Introduction we now cite a new review article (Biophysical Journal, 2024). I am not sure what more we can do to raise awareness regarding catch and hold.

(4) The figures are dense and could be better organised. Figure 2 is key but has a muddled organization. The placement of the panel label (C) makes it look like the top row (0 ns) is part of (A). Panel B- what is shown in the oval inset (not labeled or in legend). Why not show more than one view, perhaps a sequence of time points? It is confusing to change the colour of the loops in (C). Please show the individual values in D.

Figure 2 has been redone.

(5) A lot is made of the aK145 salt bridge with aD200 and the distances - but I didn't see any measurements, or time course. This part is vague to the point of having no meaning ("bridge tightening").

We present a Table of distance measurements in the SI (Figure 6-table supplement 1).

Reviewer #2 (Recommendations For The Authors):

All main comments have been given in the above review. There are a few other minor comments below.

The 4 agonists examined were acetylcholine (ACh), carbamylcholine (CCh), epibatidine (Ebt), and epiboxidine (Ebx). Could the choices be motivated for the reader?

New in Methods: the agonists are about the same size yet represent different efficiency classes (citation to companion eLife paper). One of our (unmet) objectives was to understand the structural correlates of agonist efficiency.

The authors write that state structures generated in the MD simulation were identified by aligning free energy values with those from experiments. It would be good to explain to the reader, in the introduction, how LA and HA free energies were extracted from experiments, rather than relying on them to read older papers.

In the Introduction, we say that to get G, just measure an equilibrium constant and take the log. We think it is excessive to explain in detail in this paper how to measure the equilibrium binding constants (several methods suffice). However, we have added in Methods our basic approach: measure KLA and L2 by using electrophysiology, and compute KHA from the thermodynamic cycle using L0. We think this paper is best understood in the context of its companion, also in eLife.

In all equilibrium equations of the type A to B (e.g. on page 5), rather than using "=" signs it would be much better to use equilibrium reversible arrow symbols.

It is incorporated.

Reviewer #3 (Recommendations For The Authors):

(1) Although the match in simulated vs experimental energies for two ligands was very good, the calculated energies for Ebt and Ebx were significantly different than the experiment. Are there any alternative methods for calculating binding energies from the MD simulations that could be readily compared to?

See above. We did not use more sophisticated energy calculations because we already knew the answers. Our objective was to identify states, not to calculate energies.

(2) It would be nice to see control simulations of an apo site to ensure that the conformational changes during the MD are due to the ligands and not an artifact of the way the system is set up. I am primarily asking about this as the simulation of the isolated ECDs for the binding site interface seems like it may be unhappy without the neighboring domains that would normally surround it. On that note, was the protein constrained in any way during the MD?

Apo simulation results are presented in Figure 2-figure supplement 2. The dimer interface seems to be adequate (stable).

(3) Figure 4A-B: Should the colors for m1 and m3 be reversed?

Colors have been changed and a bar chart has been added.

Reviewer #4 (Recommendations For The Authors):

(1) Although simulations are commendably run in triplicate, it is difficult in some places to discern their consistency.

(1a) Table S1 provides important quantification of deviations in different replicates and with different agonists. Please confirm that the reported values are accurate. All values reported for the epibatidine system are identical to those reported for carbamylcholine, which seems statistically improbable. Similarly, runs 1 and 3 with epiboxidine seem identical to one another, and runs 1 and 2 with acetylcholine are nearly the same.

Figure 2-Source Data 1 has been corrected.

(1b) In reference to Figure S3, the authors comment that the simulated system (one replicate with carbamylcholine) converges within 0.5 Å RMSD of a desensitized experimental structure. This seems amazing; please specify over what atoms this deviation was calculated and with reference to what alignment. It would be interesting to know the reproducibility of this remarkable convergence in additional replicates or with other ligands; for example, Figure 5 indicates that loop C transitions to a lesser extent in the context of epibatidine than other agonists.

The comparison was for the entire dimer ECD; 0.5 Å is the result. It may be worthwhile to pursue this remarkable convergence, but not in this paper. Here, we are concerned with identifying ACLA and ACHA. Similarity between ACHA and AD structures is for a different study.

(1c) For principal-component and subsequent analyses, it appears that only one trajectory was considered for each system. Please clarify whether this is the case; if so, a rationale for the selection would be helpful, and some indication of how reproducible other replicates are expected to be.

We have added new PCA results (Results, Figure 3-figure supplement 1) that show comparable principal components in other replicates.

(2) Figure 3 shows free energy landscapes defined by principal components of fluctuation in Cα positions.

(2a) Do experimental structures (e.g. PDB IDs 6UWZ, 7QL6u) project onto any of these landscapes in informative ways?

6UWZ.pdb matches well with the apo (7QKO.pdb), comparable to m1, and 7QL6.pdb with the m3.

(2b) Please indicate the meaning of colored regions in the righthand panels.

The color panels in the top left panel indicate the colored regions in the righthand panel also, which is indicative of direction and magnitude of changes with PC1 and PC2.

(2c) Please also check the legend; do the porcupine plots really "indicate the direction and magnitude of changes between PC1 and PC2," or rather between negative and positive values of each principal component?

It indicates the direction and magnitude of changes with PC1 and PC2.

(3) It would be helpful to clarify how trajectory segments were assigned to specific minima, particularly m2 and m3.

(3a) Please verify the timeframes associated with the m2 minima, reported as "20-50 ns [with acetylcholine], 50-60 ns [with carbamylcholine], 60-100 ns [with epibatidine, and] 100-120 ns [with epiboxidine]." It seems improbable that these intervals would interleave so precisely in independent systems. Furthermore, the intervals associated with acetylcholine and epiboxidine do not appear to correspond to the m2 regions indicated in Figure S8.

Times are given in Figure 4-Source Data 1 and Figure 3-figure supplement 2. The m2 classification is based on loop displacement as well as agonist orientation. For all agonists, the selection was strictly from PCA and cluster analysis.

(3b) The text (and legend to Figure 3) indicate that 180+ ns of each trajectory was assigned to m3, which seems surprisingly consistent. However, Figure S5 indicates this minimum is more variable, appearing at 160 ns with acetylcholine but at 186 ns with carbamylcholine. Please clarify.

see above: the selection was from PCA and cluster analysis. Times are in Figure 3-figure supplement 2 and also in Figure 4-Source Data 1 (none in Fig. 3 legend).

(3c) Figures 5, 6, S6, and S7 illustrate structural features of free-energy minima in each ligand system. Please clarify what is shown, e.g. a representative snapshot, centroid, or average structure from a particular prominent cluster associated with a given minimum.

They are all representative snapshots (now in Methods). Snapshots and distance measurements (Figure 6-table supplement 1) were extracted from m1, m2 and m3 plateau regions of trajectories.

(4) Figure S4 helpfully shows the behavior of a pentameric control system; however, some elements are unclear.

(4a) The 2.5-6.5 Å jump in RMSD at ~40 ns seems abrupt; can it be clarified whether this corresponds to a transition to either m2 or m3 poses, or to another feature of e.g. alignment?

Figure 2-figure supplement 4 left bottom is just the ligand. The jump is the flip, m1 to m2.

(4b) It seems difficult to reconcile the apparently bimodal distribution of states with the proposed 3-state model. Into which RMSD peak would the m2 intermediate fall?

The simulations are only to 100 ns, where we found a complete flip of the agonist represented in the histograms. This confirmed that dimer showed similar pattern as the pentamer. In depth analysis was only done only on dimers.

(4c) The top panel is labeled "Com" with a graphical legend indicating "ACh." Does this indicate the ligand or, as described in the text legend, "the pentamer" (i.e. the receptor)? For both panels, please verify whether they are calculated on the basis of center-of-mass, heavy atoms, Cα, etc.

"Com" (for complex) has been changed to system (protein+ligand).

(5) Minor concerns:

(5a) In Figures 1 and S3, correct the PDB references (6UWX and 7QL7 are not nAChRs).

They are now corrected.

(5b) In Figure 4, do all panels represent mean {plus minus} standard deviation calculated across all cluster-frames reported in Table 1?

Yes.

Also check the graphical legend in panel A: presumably the red bars correspond to m1/LA, and the blue to m3/HA?

Corrected

(5c) In the legend to Figure S1, please clarify that panel B is reproduced from Indurthi & Auerbach 2023.

This figure has been deleted.

(5d) As indicated in Figure S2, it seems surprising that the RMSF is so apparently low at the periphery, where the subunits should contact neighbors in the extracellular domain; how might the authors account for this? Specify whether these results apply to all replicates of each system.

The redness in the periphery for all four systems indicates the magnitude of fluctuation. As we focus on the orthosteric site, we highlight the loops around the agonist binding pocket and kept other regions 75% transparent. We now include Apo simulations and the dimer appears to be stable even without an agonist present.

(5e) Within each minimum in Figure S5, three "prominent" clusters appear to be colored (by heteroatom) with carbons in cyan, pink, and yellow respectively. If this is correct, note these colors in the text legend.

Colors have been added to the legend.

(5f) In Figure S6, note in the legend that key receptor sidechains are shown as spheres, with the ligand as balls-and-sticks, and that ligand conformations in both low- and high-affinity complexes are shown in both receptor states for comparison.

This is now added in the legend.

(5g) The legend to Figure S6 also notes "The agonists are as in Fig S4," but that figure contains a single replicate of a different system; please check this reference.

This has been updated to Figure 5.

(5h) In Figure S8, the colors in the epibatidine system appear different from the others.

The colors are the same for m1, m2 and m3 in all systems including epibatidine.

(5i) In Table 1, does "n clusters" indicate the number of simulation frames included in the three prominent clusters chosen for MM-PBSA analysis? Perhaps "n frames" would be more clear.

It was a good suggestion. It has now been changed to ‘n frames’

(5j) Pg 24-ln 453 presumably should read "...that separate it from m1 and m3..."

This sentence is now changed in the discussion.

eLife assessment

This useful work provides insight into agonist binding to nicotinic acetylcholine receptors, which is the stimulus for channel activation that regulates muscle contraction at the neuromuscular junction. The authors use in silico methods to explore the transient conformational change from a low to high affinity agonist-bound conformation as occurs during channel opening, but for which structural information is lacking owing to its transient nature. The evidence supporting the main conclusion that ligands flip ~180 degrees in the binding site as it transitions from a low to high affinity bound conformation is incomplete because little support is available for the starting low affinity docked conformations, and the rather approximate methods for computing binding free energies differ significantly from experimental measures for two of the four tested ligands. Nonetheless, this work presents an intriguing possibility for the nature of a transient conformational change at the agonist binding site correlated with channel opening. If the ligand flip observed in these simulations can be reproduced or verified by other studies, then this work would stand as a significant advance in our knowledge of nicotinic receptor gating.

Reviewer #1 (Public Review):

Summary:

The authors want to understand fundamental steps in ligand binding to muscle nicotinic receptors using computational methods. Overall, although the work provides new information and support for existing models of ligand activation of this receptor type, some limitations in the methods and approach mean that the findings are not as conclusive as hoped.

Strengths:

The strengths include the number of ligands tried, and the comparison to the existing mature analysis of receptor function from the senior author's lab.

Weaknesses:

The weakness are the brevity of the simulations, the concomitant lack of scope of the simulations, the lack of depth in the analysis and the incomplete relation to other relevant work. The free energy methods use seem to lack accuracy - they are only correct for 2 out of 4 ligands.

Reviewer #2 (Public Review):

Summary:

The aim of this manuscript is to use molecular dynamics (MD) simulations to describe the conformational changes of the neurotransmitter binding site of a nicotinic receptor. The study uses a simplified model including the alpha-delta subunit interface of the extracellular domain of the channel and describes the binding of four agonists to observe conformational changes during the weak to strong affinity transition.

Strength:

The 200 ns-long simulations of this model suggest that the agonist rotates about its centre in a 'flip' motion, while loop C 'flops' to restructure the site. The changes appear to reproduced across simulations and different ligands and are thus a strong point of the study.

Weaknesses:

After carrying out all-atom molecular dynamics, the authors revert to a model of binding using continuum Poisson-Boltzmann, surface area and vibrational entropy. The motivations for and limitations associated with this approximate model for the thermodynamics of binding, rather than using modern atomistic MD free energy methods (that would fully incorporate configurational sampling of the protein, ligand and solvent) could be provided. Despite this, the authors report correlation between their free energy estimates and those inferred from experiment. This did, however, reveal shortcomings for two of the agonists. The authors mention their trouble getting correlation to experiment for Ebt and Ebx and refer to up to 130% errors in free energy. But this is far worse than a simple proportional error, because -24 Vs -10 kcal/mol is a massive overestimation of free energy, as would be evident if it the authors were to instead to express results in terms of KD values (which would have error exceeding a billion fold). The MD analysis could be improved with better measures of convergence, as well as more careful discussion of free energy maps as function of identified principal components, as described below. Overall, however, the study has provided useful observations and interpretations of agonist binding that will help understand pentameric ligand-gated ion channel activation.

Main points:

Regarding the choice of model, some further justification of the reduced 2 subunit ECD-only model could be given. On page 5 the authors argue that, because binding free energies are independent of energy changes outside the binding pocket, they could remove the TMD and study only an ECD subunit dimer. While the assumption of distant interactions being small seems somewhat reasonable, provided conformational changes are limited and localised, how do we know the packing of TMD onto the ECD does not alter the ability of the alpha-delta interface to rearrange during weak or strong binding? They further write that "fluctuations observed at the base of the ECD were anticipated because the TMD that offers stability here was absent.". As the TMD-ECD interface is the "gating interface" that is reshaped by agonist binding, surely the TMD-ECD interface structure must affect binding. It seems a little dangerous to completely separate the agonist binding and gating infrastructure, based on some assumption of independence. Given the model was only the alpha and delta subunits and not the pentamer with TMD, I am surprised such a model was stable without some heavy restraints. The authors state that "as a further control we carried out MD simulation of a pentamer docked with ACh and found similar structural changes at the binding pocket compared to the dimer." Is this sufficient proof of the accuracy of the simplified model? How similar was the model itself with and without agonist in terms of overall RMSD and RMSD for the subunit interface and the agonist binding site, as well as the free energy of binding to each model to compare?

Although the authors repeatedly state that they have good convergence with their MD, I believe the analysis could be improved to convince us. On page 8 the authors write that the RMSD of the system converged in under 200 ns of MD. However, I note that the graph is of the entire ECD dimer, not a measure for the local binding site region. An additional RMSD of local binding site would be much more telling. You could have a structural isomerisation in the site and not even notice it in the existing graph. On page 9 the authors write that the RMSF in Fig.S2 showed instability mainly in loops C and F around the pocket. Given this flexibility at the alpha-delta interface, this is why collecting those regions into one group for the calculation of RMSD convergence analysis would have been useful. They then state "the final MD configuration (with CCh) was well-aligned with the CCh-bound cryo-EM desensitized structure (7QL6)... further demonstrating that the simulation had converged." That may suggest a change occurred that is in common with the global minimum seen in cryo EM, which is good, but does not prove the MD has "converged". I would also rename Fig.S3 accordingly.

The authors draw conclusions about the dominant states and pathways from their PCA component free energy projections that need clarification. It is important first to show data to demonstrate that the two PCA components chosen were dominant and accounted for most of the variance. Then when mapping free energy as a function of those two PCA components, to prove that those maps have sufficient convergence to be able to interpret them. Moreover, that if the free energies themselves cannot be used to measure state stability (as seems to be the case), that the limitations are carefully explained. First, was PCA done on all MD trajectories combined to find a common PC1 & PC2, or were they done separately on each simulation? If so, how similar are they? The authors write "the first two principal components (PC-1 and PC-2) that capture the most pronounced C. displacements". How much of the total variance did these two components capture? The authors write the changes mostly concern loop C and loop F, but which data proves this? e.g. A plot of PC1 and PC2 over residue number might help?

The authors map the -kTln rho as a free energy for each simulation as function of PC1 & PC2. It is important to reveal how well that PC1-2 space was sampled, and how those maps converged over time. The shapes of the maps and the relative depths of the wells look very different for each agonist. If the maps were sampled well and converged, the free energies themselves would tell us the stabilities of each state. Instead, the authors do not even mention this and instead talk about "variance" being the indicator of stability, stating that m3 is most stable in all cases. While I can believe 200ns could not converge a PC1-2 map and that meaningful delta G values might not be obtained from them, the issue of lack of sampling must be dealt with. On page 12 they write "Although the bottom of the well for 3 energy minima from PCA represent the most stable overall conformation of the protein, they do not convey direct information regarding agonist stability or orientation". The reasons why not must be explained; as they should do just that if the two order parameters PC1 and PC2 captured the slowest degrees of freedom for binding and sampling was sufficient. The authors write that "For all agonists and trajectories, m3 had the least variance (was most stable), again supporting convergence by 200 ns." Again the issue of actual free energy values in the maps needs to be dealt with. The probabilities expressed as -kTln rho in kcal/mol might suggest that m2 is the most stable. Instead, the authors base stability only on variance (I guess breadth of the well?), where m3 may be more localised in the chosen PC space, despite apparently having less preference during the MD (not the lowest free energy in the maps).

The motivations and justifications for use of approximate PBSA energetics instead of atomistic MD free energies should be dealt with in the manuscript, with limitations more clearly discussed. Rather than using modern all-atom MD free energy methods for relative or absolute binding free energies, the author select clusters from their identified states and do Poisson-Boltzmann estimates (electrostatic, vdW, surface area, vibrational entropy). I do believe the following sentence does not begin to deal with the limitations in that method: "there are limitations with regard to MM-PBSA accurately predicting absolute binding free energies (Genheden & Ryde, 2015; Hou et al., 2011) that depends on parameterization of the ligand (Oostenbrink et al., 2004)." What are the assumptions and limitations in taking a continuum electrostatics (presumably with parameters for dielectric constants and their assignments to regions after discarding solvent), surface area (with its assumptions and limitations) and of course assuming vibration of a normal mode can capture entropy. On page 30, regarding their vibrational entropy estimate, they write that the "entropy term provides insights into the disorder within the system, as well as how this disorder changes during the binding process". It is important that the extent of disorder captured by the vibrational estimate be discussed, as it is not obvious that it has captured entropy involving multiple minima on the system's true 3N-dimensional energy surface, and especially the contribution from solvent disorder in bound Vs dissociated states.

As discussed above, errors in the free energy estimates need to be more faithfully represented, as fractional errors are not meaningful. On page 21 the authors write "The match improved when free energy ratios rather than absolute values were compared." But a ratio of free energies is not a typical or expected measure of error in delta G. They also write "For ACh and CCh, there is good agreement between.Gm1 and GLA and between.Gm3 and GHA. For these agonists, in silico values overestimated experimental ones only by ~8% and ~25%. The agreement was not as good for the other 2 agonists, as calculated values overestimated experimental ones by ~45%(Ebt) and ~130% (Ebt). However, the fractional overestimation was approximately the same for GLA and GHA." See above comment on how this may misrepresent the error. On page 21 they write, in relation to their large fractional errors, that they "do not know the origin of this factor but speculate that it could be caused by errors in ligand parameterization". But the estimates from the PBSA approach are, by design, only approximate. Both errors in parameterisation (and their likely origin) and the approximate model used, need discussion.

Reviewer #3 (Public Review):

Summary:

The authors use docking and molecular dynamics (MD) simulations to investigate transient conformations that are otherwise difficult to resolve experimentally. The docking and simulations suggest an interesting series of events whereby agonists initially bind to the low affinity site and then flip 180 degrees as the site contracts to its high affinity conformation. This work will be of interest to the ion channel community and to biophysical studies of pentameric ligand-gated channels.

Strengths:

I find the premise for the simulations to be good, starting with an antagonist bound structure as an estimate of the low affinity binding site conformation, then docking agonists into the site and using MD to allow the site to relax to a higher affinity conformation that is similar to structures in complex with agonists. The predictions are interesting and provide a view into what a transient conformation that is difficult to observe experimentally might be like.

Weaknesses:

A weakness is that the relevance of the initial docked low affinity orientations depend solely on in silco results, for which simulated vs experimental binding energies deviate substantially for two of the four ligands tested. This raises some doubt as to the validity of the simulations. I acknowledge that the calculated binding energies for two of the ligands were closer to experiment, and simulated efficiencies were a good representation of experimental measures, which gives some support to the relevance of the in silico observations. Regardless, some of the reviewers comments regarding the simulation methodology were not seriously addressed.

Reviewer #4 (Public Review):

Summary:

In their revised manuscript "Conformational dynamics of a nicotinic receptor neurotransmitter binding site," Singh and colleagues present molecular docking and dynamics simulations to explore the initial conformational changes associated with agonist binding in the muscle nicotinic acetylcholine receptor, in context with the extensive experimental literature on this system. Their central findings are of a consistently preferred pose for agonists upon initial association with a resting channel, followed by a dramatic rotation of the ligand and contraction of a critical loop over the binding site. Principal component analysis also suggests the formation of an intermediate complex, not yet captured in structural studies. Binding free energy estimates are consistent with the evolution of a higher-affinity complex following agonist binding, with a ligand efficiency notably similar to experimental values. Snapshot comparisons provide a structural rationale for these changes on the basis of pocket volume, hydration, and rearrangement of key residues at the subunit interface.

Strengths:

Docking results are clearly presented and remarkably consistent. Simulations are produced in triplicate with each of four different agonists, providing an informative basis for internal validation. They identify an intriguing transition in ligand pose, not well documented in experimental structures, and potentially applicable to mechanistic or even pharmacological modeling of this and related receptor systems. The paper seems a notable example of integrating quantitative structure-function analysis with systematic computational modeling and simulations, likely applicable to the wider journal audience.

Weaknesses:

The response to initial review is somewhat disappointing, declining in some places to implement suggested clarifications, and propagating apparent errors in at least one table (Fig 2-source data 1). Some legends (e.g. Fig 2-supplement 4, Fig 3, Fig 4) and figure shadings (e.g. Fig 2-supplement 2, Fig 6-supplement 2) remain unclear. Apparent convergence of agonist-docked simulations towards a desensitized state (l 184) is difficult to interpret in absence of comparative values with other states, systems, etc. In more general concerns, aside from the limited timescales (200 ns) that do not capture global rearrangements, it is not obvious that landscapes constructed on two principal components to identify endpoint and intermediate states (Fig 3) are highly robust or reproducible, nor whether they relate consistently to experimental structures.

Author Response

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

Thank you and the two reviewers for the thorough review of our manuscript. We thank you very much for the positive evaluation of our manuscript and your encouragement to continue in this fascinating topic. In this version we made minor changes in the text to address the comments and suggestion of the second reviewer and increase the clarity of the text.

Reviewer #2 Recommendation to the authors

We thank the reviewer for the sharp comments that help us improve the clarity of the paper. Below we list the changes we made to correct and revise the paper in accordance to the reviewer’s comments.

(1) Line 90. Isn't the genus Paracentrotus?

Yet it is, thank you. We corrected the typo.

(2) Figure 1 and supplementary figure 2. To this reviewer supplementary Figure 2 doesn't really help the story as written in the paragraph from line 96-110. You want to report expression of ROCK in skeletogenic cells. You do that quite well in Figure 1. Since Fig. S2 reports whole embryo expression of ROCK when only 5% of the cells in the embryo are the subject of interest here, and the Axitinib is selective, presumably for skeletogenic cells, the relative lack of effect in Fig. S2 is not surprising and again, doesn't really help the theme you wish to establish by focusing on the role of ROCK in skeletogenic cells over time. If anything, the data reported in Fig. S2 shows that perturbation of VEGF signaling has very little effect embryo-wide, while Fig. 1 shows that perturbation of VEGF signaling has a noticeable effect on ROCK expression in skeletogenic cells. If you choose to keep Fig. S2, I recommend that you indicate that embryo-wide vs skeletogenic cell difference more succinctly than given at present. It will also strengthen your paragraph in lines 110-127.

The importance of the western blot presented in Fig. S2 is to validate that the antibody recognizes a protein of the expected size. This strengthen the credibility of this commercial antibody to detect the sea urchin ROCK protein. We agree with the reviewer that the fact that the skeletogenic cells are less than 5% of the embryonic cells is important to explain why we didn’t see an affect of VEGFR inhibition in the western blot, and we changed the text to express it (lines 108-111): “Yet, this measurement was done on proteins extracted from whole embryos, of which the skeletogenic cells, where VEGFR is active, are less than 5% of the total cell mass (42). We therefore wanted to study the spatial expression of ROCK and specifically, its regulation in the skeletogenic cells.”

(3) Comparison of Fig. 2 and Fig. S3. To me the reader is confused when Fig. S3 is 33hpf as reported in the text (but not in the figure legend), and Fig. 2 shows 2 day old embryos - on the figure and figure legend but not in the text. So, the reader sees the text indicating 33hpf and looks around and the figure 2 says 2dpf. Does that mean 33hpf = 2dpf, the reader is thinking. To clarify, I suggest including the 2dpf in the text or simply drop the time in the text and report it in the two figures. Further, in the middle of the paragraph 130-143 you switch from reporting on Fig.S3 to Fig. 2, yet the reader doesn't know that. The reader is still looking at Fig. S3. The problem here is that at 33hpf the skeleton doesn't yet show the reduction or abnormalities that are shown later at 2dpf in Fig. 2. In clarifying this paragraph both the reduction in ROCK expression and the subsequent alterations in growth and patterning of the skeleton will be clear to the reader.

Thank you for raising this point. We added in the caption of Fig. S3 that the measurements were done in 33hpf. We also added in the text, that the observations of the skeletogenic phenotypes were done at 2dpf (48hpf). We made a break between the first paragraph discussing Fig. S3 and the paragraph discussing Fig. 2.

(4) The experiment with Y27632, an inhibitor of ROCK, is significantly improved in this revision. The concern earlier was the possibility that at the concentration used there might be off-target effects since other kinases are affected by higher concentrations of this selective inhibitor. The authors have modified this component of the paper and performed experiments at lower concentrations where other reports indicate the inhibitor is highly selective for ROCK, and they still demonstrate an inhibition of skeletal production. This, plus the added citations greatly increases confidence that this inhibition is selective for ROCK, thus enabling a stronger conclusion that ROCK has a role in skeletal growth and patterning.

Thank you for asking us to test this lower concentration which improved the credibility of our findings.

Line 239 - should be: indicating instead of indicting We corrected that.

(5) Line 402-403."The first step in generating the sea urchin spicules is the construction of the spicule cavity, a membrane filled with calcium carbonate and coated with F-actin (Fig. 8A)". I suggest more precise language. The way this now reads (above) is that somehow the spicule cavity is a membrane and that membrane is filled with CaCO3. And further the membrane is coated with F-actin. Isn't the spicule cavity what is filled with CaCO3? And isn't that cavity surrounded by a membrane? And the F-actin must be in the cortex of the cell since there is very little cytoplasm associated with the pseudopodial extensions that surround the spicule.

We change this sentence to: “The first step in generating the sea urchin spicules is the construction of the spicule cavity where the mineral is engulfed in a membrane coated with F-actin” (lines 403-404). Our observations show that F-actin is enriched around the spicule cavity. It could be an extension of the cell cortex, but we did not prove it, so we prefer to simply describe what we saw.

Line 405-408. Thank you for putting in this unknown. It is important to point out that while you've shown that ROCK contributes to regulation of actomyosin, it is not clear whether this is direct or indirect. You have also shown that ROCK somehow contributes to regulation of the GRN that leads to skeletogenesis. Thus, your data are consistent in showing that ROCK perturbation cripples normal skeletogenesis both via morpholino and with a selective inhibitor. Your last part of the discussion then offers speculation as to what might be affected specifically. That discussion sets the stage for digging even deeper to identify specific targets of ROCK activity.

Thank you, we agree with you that there is an exciting road ahead of us!

eLife assessment

This valuable study addresses the role of Rho-associated coiled-coil kinase (ROCK) and the cytoskeleton in the initiation and growth of the calcified endoskeleton of sea urchin embryos. Perturbation by two independent approaches (a morpholino and a selective inhibitor) provides convincing evidence that ROCK participates both in actomyosin regulation and in the gene regulatory network that controls skeletogenesis. Exciting areas of future work will be to elucidate the mechanisms by which ROCK influences gene expression and to further dissect the role of the cytoskeleton in mineralization.

Reviewer #1 (Public Review):

Using a pharmacological and knock-down approach, the authors could demonstrate that ROCK activity is required for the normal development of the larval skeleton. The presence of ROCK in the pluteus stage depends on the activity of VEGF that is responsible for the formation of the tubular syncytial sheath of the calcifying primary mesenchyme cells in which the skeleton forms. The importance of ROCK in skeleton formation was confirmed in cell culture experiments, demonstrating that ROCK inhibition leads to decreased elongation and abnormal branching of spicules. µCT analyses underline this finding demonstrating that the inhibition of ROCK mainly affects elongation of spicules while growth in girth is little affected. F-actin labeling experiments could demonstrate that ROCK inhibition interferes with the organization of the actomyosin network in the early phase of skeleton formation, while f-actin organization in the tips of the elongating spicule is unaffected by the pharmacological inhibition of ROCK. Finally, ROCK inhibition strongly affects the expression of major regulatory and calcification-related genes in the calcifying cells. Based on these findings the authors propose a model for the regulatory interaction between the skeletogenic GRN, ROCK and the f-actin system relevant for skeletogenesis.

Comments on revised version:

In their manuscript Hijaze et al. adequately addressed the majority of my previous concerns in a satisfactory manner. In particular, they validated their morpholino knock-down experiments by explaining how they determined the optimal concentrations and provided an immunohistological evidence for the reduction in ROCK protein abundance. The authors also added new antibody stainings providing evidence that ROCK and F-actin do not interact directly but likely through other kinases that modulate f-actin, and that the localization of f-actin at the spicule tips remains unaffected by the knock-down. In addition, the authors revised their discussion to not overstate their observations, and by focusing on the potential mechanisms by which ROCK may affect biomineralization (i.e. mechano sensing and exocytosis of vesicles). Here I would like to add, that f-actin mediated exocytosis does not necessarily target mineral baring vesicles but may also promote the exocytosis of matrix proteins that are essential for the normal formation of the spicules and that are an integral component of other biominerals, as well. I strongly encourage the authors to continue on this exciting research, including the development of methods to analyze the molecular mechanisms that control vesicular trafficking in mineralizing systems.

Reviewer #2 (Public Review):

This project is on the role of ROCK in skeletogenesis during sea urchin development. That skeleton is produced by a small number of cells in the embryo with signaling inputs from the ectoderm providing patterning cues. The skeleton is built from secretion of CaCO3 by the skeletogenic cells. The authors conclude that ROCK is involved in the regulation of skeletogenesis with a role both in regulating actomyosin in the process, and in the gene regulatory network (GRN) underlying the entire sequence of events.

The strength of the paper is that they show in detail how perturbations of ROCK results in abnormal actomyosin activity in the skeletogenic cells, and they show alterations both in expression of transcription factors of the GRN, and expression of genes involved in assembly of the skeletal matrix. Two different approaches lead to this conclusion: morpholino perturbations and the actions of a selective inhibitor of the kinase activity. Thus, they achieved their goal which was to test the hypothesis that ROCK is involved in the process of skeletogenesis. Those tests support the hypothesis with data that was quantitatively significant.

The discussion was transparent regarding where the analysis ended and where the next phase of work should begin. While actomyosin involvement was altered when ROCK was perturbed, it isn't known how direct or indirect the role of ROCK might be. Also, while the regulatory input to spicule initiation and growth is affected when ROCK is inhibited, it isn't clear exactly where ROCK is involved.

Reviewer #2 (Public Review):

Summary:

In this paper, the authors set out to better understand the mechanism by which the FtsZ-associated protein ZapD crosslinks FtsZ filaments to assemble a large scale cytoskeletal assembly. For this aim, they use purified proteins in solution and a combination of biochemical, biophysical experiments and cryo-EM. The most significant finding of this study is the observation of FtsZ toroids that form at equimolar concentrations of the two proteins.

Strengths:

Many experiments in this paper confirm previous knowledge about ZapD. For example, it shows that ZapD promotes the assembly of FtsZ polymers, that ZapD bundles FtsZ filaments, that ZapD forms dimers and that it reduces FtsZ's GTPase activity.

The most novel discovery is the observation of different assemblies as a function of ZapD:FtsZ ratio. In addition, using CryoEM to describe the structure of toroids and bundles, the papers provides some information about the orientation of ZapD in relation to FtsZ filaments. For example, they found that the organization of ZapD in relation to FtsZ filaments is "intrinsic heterogeneous" and that FtsZ filaments were crosslinked by ZapD dimers pointing in all directions. The authors conclude that it is this plasticity that allows for the formation of toroids and its stabilization. Unfortunately, a high-resolution structure of the protein organization was not possible.

Weaknesses:

While the data is convincing, their interpretation has some substantial weaknesses that the authors should address for the final version of this paper.

For example, as the authors are the first to describe FtsZ-ZapD toroids, a discussion why this has not been observed in previous studies would be very interesting, i.e. is it due to buffer conditions, sample preparation?

At parts of the manuscript, the authors try a bit too hard to argue for the physiological significance of these toroids. This, however, is at least very questionable, because:<br /> The typical diameter is in the range of 0.25-1.0 μm, which requires some flexibility of the filaments to be able to accommodate this. It's difficult to see how a FtsZ-ZapD toroid, which appears to be quite rigid with a narrow size distribution of 502 nm {plus minus} 55 nm could support cell division rather than stalling it at that cell diameter. which the authors say is similar to the E. coli cell.

For cell division, FtsZ filaments are recruited to the membrane surface via an interaction of FtsA or ZipA the C-terminal peptide of FtsZ. As ZapD also binds to this peptide, the question arises who wins this competition or where is ZapD when FtsZ is recruited to the membrane surface? Can such a toroidal structure of FtsZ filaments form on the membrane surface? Additional experiments would be helpful, but a more detailed discussion on how the authors think ZapD could act on membrane-bound filaments would be essential.

The authors conclude that the FtsZ filaments are dynamic, which is essential for cell division. But the evidence for dynamic FtsZ filaments within these toroids seems rather weak, as it is solely the partial reassembly after addition of GTP. As ZapD significantly slows down GTP hydrolysis, I am not sure it's obvious to make this conclusion.

On a similar note, on page 5 the authors claim that ZapD would transiently interact with FtsZ filaments. What is the evidence for this? They also say that this transient interaction could have a "mechanistic role in the functionality of FtsZ macrostructures." Could they elaborate?

The author should also improve in putting their findings into the context of existing knowledge. For example:

The authors observe a straightening of filament bundles with increasing ZapD concentration. This seems consistent with what was found for ZapA, but this is not explicitly discussed (Caldas et al 2019)

A paragraph summarizing what is known about the properties of ZapD in vivo would be essential: i.e. what has been found regarding its intracellular copy number, location and dynamics?

In the introduction, the authors write that "GTP binding and hydrolysis induce a conformational change in each monomer that modifies its binding potential, enabling them to follow a treadmilling behavior". This seems inaccurate, as shown by Wagstaff et al. 2022, the conformational change of FtsZ is not associated with the nucleotide state. In addition, they write that FtsZ polymerization depends on the GTPase activity. It would be more accurate to write that polymerization depends on GTP, and disassembly on GTPase activity.

On page 2 they also write that "the mechanism underlying bundling of FtsZ filaments is unknown". I would disagree, the underlying mechanism is very well known (see for example Schumacher, MA JBC 2017), but how this relates to the large-scale organization of FtsZ filaments was not clear.

The authors describe the toroid as a dense 3D mesh, how would this be compatible with the Z-ring and its role for cell division? I don't think this corresponds to the current model of the Z-ring (McQuillen & Xiao, 2020). Apart from the fact it's a ring, I don't think the organization of FtsZ obviously similar to the current of the Z-ring in the bacterial cell, in particular because it's not obvious how FtsZ filaments can bind ZapD and membrane anchors simultaneously.

The authors write that "most of these modulators" interact with FtsZ's CTP, but then later that ZapD is the only Zap protein that binds CTP. This seems to be inconsistent. Why not write that membrane anchors usually bind the CTP, most Zaps do not, but ZapD is the exception?

I also have some comments regarding the experiments and their analysis:

Regarding cryoET: the filaments appear like flat bands, even in the absence of ZapD, which further elongates these bands. Is this due to an anisotropic resolution? This distortion makes the conclusion that ZapD forms bi-spherical dimers unconvincing.

The authors say that the cryoET visualization provides crucial information on the length of the filaments within this toroid. How long are they? Could the authors measure it?

Regarding the dimerization mutant of ZapD: there is actually no direct confirmation that mZapD is monomeric. Did the authors try SEC MALS or AUC? Accordingly, the statement that dimerization is "essential" seems exaggerated (although likely true).

What do the authors mean that toroid formation is compatible with robust persistence length? I.e. What does robust mean? It was recently shown that FtsZ filaments are actually surprisingly flexible, which matches well the fact that the diameter of the Z-ring must continuously decrease during cell division (Dunajova et al Nature Physics 2023).

the authors claim that their observations suggest „that crosslinkers ... allows filament sliding in an organized fashion". As far as I know there is no evidence of filament sliding, as FtsZ monomers in living cells and in vitro are static.

What is the „proto-ring FtsA protein"?

The authors refer to „increasing evidence" for „alternative network remodling mechanisms that do not rely on chemical energy consumption as those in which entropic forces act through diffusible crosslinkers, similar to ZapD and FtsZ polymers." A reference should be given, I assume the authors refer to the study by Lansky et al 2015 of PRC on microtubules. However, I am not sure how the authors made the conclusion that this applies to FtsZ and ZapD, on which evidence is this assumption based?

Some inconsistencies in supplementary figure 3: The normalized absorbances in panel a do not seem to agree with the absolute absorbance shown in panel e, i.e. compare maximum intensity for ZapD = 20 µM and 5 µM in both panels.

It's not obvious to me why the structure formed by ZapD and FtsZ disassembles after some time even before GTP is exhausted, can the authors explain? As the structures disassemble, how is the "steady-state turbidity" defined? Do the structures also disassemble when they use a non-hydrolyzable analog of GTP?

Conclusion:

Despite some weaknesses in the interpretation of their findings, I think this paper will likely motivate other structural studies on large scale assemblies of FtsZ filaments and its associated proteins. A systematic comparison of the effects of ZapA, ZapC and ZapD and how their different modes of filament crosslinking can result in different filament networks will be very useful to understand their individual roles and possible synergistic behavior.

eLife assessment

The formation of the Z-ring at the time of bacterial cell division interests researchers working towards understanding cell division across all domains of life. The manuscript by Jasnin et al reports the cryoET structure of toroid assembly formation of FtsZ filaments driven by ZapD as the cross linker. The findings are important and have the potential to open a new dimension in the field, but the evidence to support these exciting claims is currently inadequate.

Reviewer #1 (Public Review):

Summary:

The major result in the manuscript is the observation of the higher order structures in a cryoET reconstruction that could be used for understanding the assembly of toroid structures. The cross-linking ability of ZapD dimers result in bending of FtsZ filaments to a constant curvature. Many such short filaments are stitched together to form a toroid like structure. The geometry of assembly of filaments - whether they form straight bundles or toroid like structures - depends on the relative concentrations of FtsZ and ZapD.

Strengths:

In addition to a clear picture of the FtsZ assembly into ring-like structures, the authors have carried out basic biochemistry and biophysical techniques to assay the GTPase activity, the kinetics of assembly, and the ZapD to FtsZ ratio.

Weaknesses:

The discussion does not provide an overall perspective that correlates the cryoET structural organisation of filaments with the biophysical data.

The crosslinking nature of ZapD is already established in the field. The work carried out is important to understand the ring assembly of FtsZ. However, the availability of the cryoET observations can be further analysed in detail to derive many measurements that will help validate the model, and obtain new insights.

Reviewer #3 (Public Review):

Summary:

The authors provide the first image analysis by cryoET of toroids assembled by FtsZ crosslinked by ZapD. Previously toroids of FtsZ alone have been imaged only in projection by negative stain EM. The authors attempt to distinguish ZapD crosslinks from the underlying FtsZ filaments. I did not find this distinction convincing, especially because it seems inconsistent with the 1:1 stoichiometry demonstrated by pelleting. I was intrigued by one image showing straight filament pairs, which may suggest a new model for how ZapD crosslinks FtsZ filaments.

Strengths:

(1) The first image analysis of FtsZ toroids by cryoET.<br /> (2) The images are accompanied by pelleting assays that convincingly establish a 1:1 stoichiometry of FtsZ:ZapD subunits.<br /> (3) Fig. 5 shows an image of a pair of FtsZ filaments crosslinked by ZapD. This seems to have higher resolution than the toroids. Importantly, it suggests a new model for the structure of FtsZ-ZapD that resolves previously unrecognized conflicts. (This is discussed below under weaknesses, because it is so far only supported by a single image.)

Weaknesses:

This paper reports a study by cryoEM of polymers and bundles assembled from FtsZ plus ZapD. Although previous studies by other labs have focused on straight bundles of filaments, the present study found toroids mixed with these straight bundles, and they focused most of their study on the toroids. In the toroids they attempt to delineate FtsZ filaments and ZapD crosslinks. A major problem here is with the stoichiometry. Their pelleting assays convincingly established a stoichiometry of 1:1, while the mass densities identified as ZapD are sparse and apparently well below the number of FtsZ (FtsZ subunits are not resolved in the reconstructions, but the continuous sheets or belts seem to have a lot more mass than the identified crosslinks.) Apart from the stoichiometry I don't find the identification of crosslinks to be convincing. It is missing an important control - cryoET of toroids assembled from pure FtsZ, without ZapD.

However, if I ignore these and jump to Fig. 5, I think there is an important discovery that resolves controversies in the present study as well as previous ones, controversies that were not even recognized. The controversy is illustrated by the Schumacher 2017 model (their Fig. 7), which is repeated in a simplified version in Fig. 1a of the present mss. That model has a two FtsZ filaments in a plane facing ZapD dimers which bridge them. In this planar model the C-terminal linker, and the ctd of FtsZ that binds ZapD facing each other and the ZapD in the middle, with. The contradiction arises because the C-terminus needs to face the membrane in order to attach and generate a bending force. The two FtsZ filaments in the planar model are facing 90{degree sign} away from the membrane. A related contradiction is that Houseman et al 2016 showed that curved FtsZ filaments have the C terminus on the outside of the curve. In a toroid the C termini should all be facing the outside. If the paired filaments had the C termini facing each other, they could not form a toroid because the two FtsZ filaments would be bending in opposite directions.

Fig. 5 of the present mss seems to resolve this by showing that the two FtsZ filaments and ZapD are not planar, but stacked. The two FtsZ filaments have their C termini facing the same direction, let's say up, toward the membrane, and ZapD binds on top, bridging the two. The spacing of the ctd binding sites on the Zap D dimer is 6.5 nm, which would fit the ~8 nm width of the paired filament complex observed in the present cryoEM (Fig S13). In the Schumacher model the width would be about 20 nm. Importantly, the stack model has the ctd of each filament facing the same direction, so the paired filaments could attach to the membrane and bend together (using ctd's not bound by ZapD). Finally, the new arrangement would also provide an easy way for the complex to extend from a pair of filaments to a sheet of three or four or more.

A problem with this new model from Fig. 5 is that it is supported by only a single example of the paired FtsZ-ZapD complex. If this is to be the basis of the interpretation, more examples should be shown. Maybe examples could be found with three or four FtsZ filaments in a sheet.

What then should be done with the toroids? I am not convinced by the identification of ZapD as "connectors." I think it is likely that the ZapD is part of the belts that I discuss below, although the relative location of ZapD in the belts is not resolved. It is likely that the resolution in the toroid reconstructions of Fig. 4, S8,9 is less than that of the isolated pf pair in Fig. 5c.

Importantly, If the authors want to pursue the location of ZapD in toroids, I suggest they need to compare their ZapD-containing toroids with toroids lacking ZapD. Popp et al 2009 have determined a variety of solution conditions that favor the assembly of toroids by FtsZ with no added protein crosslinker. It would be very interesting to investigate the structure of these toroids by the present cryoEM methods, and compare them to the FtsZ-ZapD toroids. I suspect that the belts seen in the ZapD toroids will not be found in the pure FtsZ toroids, confirming that their structure is generated by ZapD.

eLife assessment

The manuscript reports on an important comparison of a range of approved clinical inhibitors for BTK used for the treatment of chronic lymphocytic leukemia (CLL). The authors provide solid evidence for their claims, using a combination of HDX-MS and NMR spectroscopy. The novelty is that this study also seeks to evaluate resistance mutation bias. The scope of the study is highly exciting but would benefit from a clear link of the biophysical studies to the functional assays - specifically nucleotide binding.

Reviewer #1 (Public Review):

Summary:

The work by Joseph et al "Impact of the clinically approved BTK inhibitors on the conformation of full-length BTK and analysis of the development of BTK resistance mutations in chronic lymphocytic leukemia" seeks to comparatively analyze the effect of a range of covalent and noncovalent clinical BTK inhibitors upon BTK conformation. The novel aspect of this manuscript is that it seeks to evaluate the differential resistance mutations that arise distinctly from each of the inhibitors.

Strengths:

This is an exciting study that builds upon the fundamental notion of ensemble behavior in solutions for enzymes such as BTK. The HDX-MS and NMR experiments are adequately and comprehensively presented.

Weaknesses:

While I commend the novelty of the study, the absence of important controls greatly tempers my enthusiasm for this work. As stated in the abstract, there are no broad takeaways for how resistance mutation bias operated from this study, although the mechanism of action of 2 common resistance mutations is useful. How these 2 resistance mutations connect to ensemble behavior, is not obvious. This is partly because BTK does not populate just binary "open"/"closed" conformations, but there are likely multiple intermediate conformations. Each inhibitor appears to preferentially "select" conformations by the authors' own assessment (line 236) and this carries implications for the emergence of resistance mutations. The most important control that would help is to use ADP or nonhydrolyzable and ATP as a baseline to establish the "inactive" and "active" conformations. All of the HDX-MS and NMR studies use protein that has no nucleotide present. A major question that remains is whether each of the inhibitors preferentially favors/blocks ADP or ATP binding. This then means it is not equivalent to correlate functional kinase assay conditions with either HDX-MS or NMR experiments.

Reviewer #2 (Public Review):

Summary:

Previous NMR and HDX-MS studies on full-length (FL) BTK showed that the covalent BTKi, ibrutinib, causes long-range effects on the conformation of BTK consistent with disruption of the autoinhibited conformation, based on HDX deuterium uptake patterns and NMR chemical shift perturbations. This study extends the analyses to four new covalent BTKi, acalabrutinib, zanubrutinib, tirabrutinib/ONO4059, and a noncovalent ATP competitive BTKi, pirtobrutinib/LOXO405.

The results show distinct conformational changes that occur upon binding each BTKi. The findings show consistent NMR and HDX changes with covalent inhibitors, which move helix aC to an 'out' position and disrupt SH3-kinase interactions, in agreement with X-ray structures of the BTKi complexed with the BTK kinase domain. In contrast, the solution measurements show that pirtobrutinib maintains and even stabilizes the helix aC-in and autoinhibited conformation, even though the BTK:pritobrutinib crystallizes with helix aC-out. This and unexpected variations in NMR and HDX behavior between inhibitors highlight the need for solution measurements to understand drug interactions with the full-length BTK. Overall the findings present good evidence for allosteric effects by each BTKi that induce distal conformational changes which are sensitive to differences in inhibitor structure.

The study goes on to examine BTK mutants T474I and L528W, which are known to confer resistance to pirtobrutinib, zanubritinib, and tirabrutinib. T474I reduces and L528W eliminates BTK autophosphorylation at pY551, while both FL-BTK-WT and FL-BTK-L528W increase HCK autophosphorylation and PLCg phosphorylation. These show that mutants partially or completely inactivate BTK and that inactive FL-BTK can activate HCK, potentially by direct BTK-HCK interactions. But they do not explain drug resistance. However, HDX and NMR show that each mutant alters the effects of BTKi binding compared to WT. In particular, T474I alters the effects of all three inhibitors around W395 and the activation loop, while L528W alters interactions around W395 with tirabrutinib and pirtobrutinib, and does not appear to bind zanubrutinib at all. The study concludes that the mutations might block drug efficacy by reducing affinity or altering binding mode.

Strengths:

The work presents convincing evidence that BTK inhibitors alter the conformation of regions distal to their binding sites, including those involved in the SH3-kinase interface, the activation loop, and a substrate binding surface between helix aF and helix aG. The findings add to the growing understanding of allosteric effects of kinase inhibitors, and their potential regulation of interactions between kinase and binding proteins.

Weaknesses:

The interpretation of HDX, NMR, and kinase assays is confusing in some places, due to ambiguity in quantifying how much kinase is bound to the inhibitor. It would be helpful to confirm binding occupancy, in order to clarify if mutants lower the amount of BTK complexed with BTKi as implied in certain places, or if they instead alter the binding mode. In addition, the interpretation of the mutant effects might benefit from a more detailed examination of how each inhibitor occupies the ATP pocket and how substitutions of T474 and L528 with Ile and Trp respectively might change the contacts with each inhibitor.

eLife assessment

In this interesting study, Drożdżyk and colleagues analyze the ability of placental CALHM orthologs to form stable complexes, identifying that CALHM2 and CALHM4 form heterooligomeric channels. The authors then determine cryo-EM structures of heterooligomeric CALHM2 and CALHM4 that reveal a distinct arrangement in which the two orthologs can interact, but preferentially segregate in the channel. This is an important study; the data provide compelling support for the interpretations and overall, the work is clearly described.

Reviewer #1 (Public Review):

The Calcium Homeostasis Modulators (CALHM) are a family of large pore channels, of which the physiological role of CALHM1 and 3 is well understood, in particular their key role in taste sensation via the release of the neurotransmitter ATP. The activation mechanism of CALHM1 involves membrane depolarization and a decrease in extracellular Ca concentration, allowing the passage of large cellular metabolites. However, the activation mechanism and physiological roles of other family members are much less well understood. Many structures of homomeric CALHM proteins have been determined, revealing distinct oligomeric assemblies despite a common transmembrane domain topology. CALHM1 and 3 have been shown functionally to form heteromeric assemblies with properties distinct from those of homomeric CALHM1. However, the structural basis of heteromeric CALHM1 and 3 remains unexplored.

In this paper, Drozdzyk et al. present an important study on the structures of heteromeric channels composed of CALHM2 and CALHM4, extending the structural understanding of the CALHM family beyond homomeric channels. The study relies primarily on cryo-EM. Despite the inherent challenges of structural determination due to the similar structural features of CALHM2 and CALHM4, the authors innovatively use synthetic nanobodies to distinguish between the subunits. Their results show a broad distribution of different heteromeric assemblies, with CALHM4 conformation similar to its homomeric form and CALHM2 conformation influenced by its proximity to CALHM4, and provide detailed insights into the interaction between CALHM2 and CALHM4.

The manuscript is well-structured and presents clear results that support the conclusions drawn. The discovery of heteromeric CALHM channels, although currently limited to an overexpressed system, represents a significant advance in the field of large-pore channels and will certainly encourage further investigation into the physiological relevance and roles of heteromeric CALHM channels. The manuscript would benefit from further insight into the functional properties of these heteromeric channels. However, this is not a weakness as the identification of precise activation stimuli for CALHM2 and 4 is beyond the scope of this work.

A challenge noted is the wide distribution of heteromeric assemblies in the 3D classification, resulting in insufficient particles for high-resolution structure determination of each assembly. The authors choose to combine particles from assemblies with 2-4 copies of CALHM4, which reveals the interface between CALHM2 and 4 but may compromise the quality of structural details. I recommend an alternative data processing strategy. First, refine particles with 2-4 CALHM4 subunits with symmetry imposed. This is followed by symmetry expansion, signal subtraction of two adjacent subunits, and subsequent classification and refinement of the subtracted particles. This approach, while not guaranteed, can potentially provide a clearer definition of CALHM2 and CALHM4 interfaces and show whether CALHM2 subunits adopt different conformations based on their proximity to CALHM4 subunits.

Reviewer #2 (Public Review):

Summary:

The authors identified that two of the placental CALHM orthologs, CALHM2 and CALHM4 can form heterooligomeric channels that are stable following detergent solubilization. By adding fiducial markers that specifically recognize either CALHM2 or CALHM4, the authors determine a cryo-EM density map of heterooligomeric CALHM2/CALHM4 from which they can determine how the channel is assembled. Surprisingly, the two orthologs segregate into two distinct segments of the channel. This segregation enables the interfacial subunits to ease the transition between the preferred conformations of each ortholog, which are similar to the confirmation that each ortholog adopts in homooligomeric channels.

Strengths:

Through the use of fiducial markers, the authors can clearly distinguish between the CALHM2 and CALHM4 promoters in the heterooligomeric channels, strengthening their assignment of most of the promoters. The authors take appropriate caution in identifying two subunits that are likely a mix of the two orthologs in the channel.

Weaknesses:

Despite the authors' efforts, no currents could be observed that corresponded to CALHM2/CALHM4 channels and thus the functional effect of their interaction is not known.