Author response:

eLife assessment

This study is a detailed investigation of how chromatin structure influences replication origin function in yeast ribosomal DNA, with focus on the role of the histone deacetylase Sir2 and the chromatin remodeler Fun30. Convincing evidence shows that Sir2 does not affect origin licensing but rather affects local transcription and nucleosome positioning which correlates with increased origin firing. However, the evidence remains incomplete as the methods employed do not rigorously establish a key aspect of the mechanism, fully address some alternative models, or sufficiently relate to prior results. Overall, this is a valuable advance for the field that could be improved to establish a more robust paradigm.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper presents a mechanistic study of rDNA origin regulation in yeast by SIR2. Each of the ~180 tandemly repeated rDNA gene copies contains a potential replication origin. Early-efficient initiation of these origins is suppressed by Sir2, reducing competition with origins distributed throughout the genome for rate-limiting initiation factors. Previous studies by these authors showed that SIR2 deletion advances replication timing of rDNA origins by a complex mechanism of transcriptional de-repression of a local PolII promoter causing licensed origin proteins (MCMcomplexes) to re-localize (slide along the DNA) to a different (and altered) chromatin environment. In this study, they identify a chromatin remodeler, FUN30, that suppresses the sir2∆ effect, and remarkably, results in a contraction of the rDNA to about one-quarter it's normal length/number of repeats, implicating replication defects of the rDNA. Through examination of replication timing, MCM occupancy and nucleosome occupancy on the chromatin in sir2, fun30, and double mutants, they propose a model where nucleosome position relative to the licensed origin (MCM complexes) intrinsically determines origin timing/efficiency. While their interpretations of the data are largely reasonable and can be interpreted to support their model, a key weakness is the connection between Mcm ChEC signal disappearance and origin firing. While the cyclical chromatin association-dissociation of MCM proteins with potential origin sequences may be generally interpreted as licensing followed by firing, dissociation may also result from passive replication and as shown here, displacement by transcription and/or chromatin remodeling.

While it is true that both transcription and passive replication can cause the signal of MCM-ChEC to disappear, neither can cause selective disappearance of the displaced complex without affecting the non-displaced complex.  Indeed, in the case of transcription, RNA polymerase transcribing C-pro would have to first dislodge the normally positioned MCM complex before even reaching the displaced complex.  Furthermore, deletion of FUN30 leads to both more C-pro transcription and less disappearance of the displaced MCM complex.  It is important to keep in mind that this cannot somehow reflect continuous replenishment of displaced MCMs with newly loaded MCMs, since the cells are in S phase and licensing is restricted to G1. 

Moreover, linking its disappearance from chromatin in the ChEC method with such precise resolution needs to be validated against an independent method to determine the initiation site(s). Differences in rDNA copy number and relative transcription levels also are not directly accounted for, obscuring a clearer interpretation of the results.

Copy number reduction of the magnitude caused by deletion of SIR2 and FUN30 does not suppress the sir2D effect (i.e. early replication of the rDNA), but rather exacerbates it.  In particular, deletion of SIR2 and FUN30 causes the rDNA to shrink to approximately 35 copies.  Kwan et al., 2023 (PMID: 36842087) have shown that reduction of rDNA copy number to 35 causes a dramatic acceleration of rDNA replication in a SIR2 strain.  Thus, the effect of rDNA size on replication timing reinforces our conclusion that deletion of FUN30 suppresses rDNA replication.

However, to address this concern directly, in the revision we will include 2 D gels in fob1 strains with equal number of repeats that allows to conclude that the effect of FUN30 deletion in suppressing rDNA origin firing is independent of either rDNA size or FOB1. The figure of the critical 2 D gels is shown below in the reply to reviewer 2.

Nevertheless, this paper makes a valuable advance with the finding of Fun30 involvement, which substantially reduces rDNA repeat number in sir2∆ background. The model they develop is compelling and I am inclined to agree, but I think the evidence on this specific point is purely correlative and a better method is needed to address the initiation site question. The authors deserve credit for their efforts to elucidate our obscure understanding of the intricacies of chromatin regulation. At a minimum, I suggest their conclusions on these points of concern should be softened and caveats discussed. Statistical analysis is lacking for some claims.

Strengths are the identification of FUN30 as suppressor, examination of specific mutants of FUN30 to distinguish likely functional involvement. Use of multiple methods to analyze replication and protein occupancies on chromatin. Development of a coherent model.

Weaknesses are failure to address copy number as a variable; insufficient validation of ChEC method relationship to exact initiation locus; lack of statistical analysis in some cases. 

The two potential initiation sites that one would monitor (non-displaced and displaced) are separated by less than 150 base pairs, and other techniques simply do not have the resolution necessary to distinguish such differences.  Furthermore, as we suggest in the manuscript, our results are consistent with a model in which it is only the displaced MCM complex that is activated, whether in sir2 or WT.  If no genotype-dependent difference in initiation sites is even expected, it would be hard to interpret even the most precise replication-based assays.  However, the reviewer is correct that this is a novel technique and that confirmation with a well-established technique is comforting, therefore we are performing ChIP experiments to corroborate, to the extent possible, the conclusions that we reached with ChEC. 

We appreciate the reviewer pointing out that some statistical analyses were lacking, and we will correct this in a revised manuscript.

Additional background and discussion for public review:

This paper broadly addresses the mechanism(s) that regulate replication origin firing in different chromatin contexts. The rDNA origin is present in each of ~180 tandem repeats of the rDNA sequence, representing a high potential origin density per length of DNA (9.1kb repeat unit). However, the average origin efficiency of rDNA origins is relatively low (~20% in wild-type cells), which reduces the replication load on the overall genome by reducing competition with origins throughout the genome for limiting replication initiation factors. Deletion of histone deacetylase SIR2, which silences PolII transcription within the rDNA, results in increased early activation or the rDNA origins (and reduced rate of overall genome replication). Previous work by the authors showed that MCM complexes loaded onto the rDNA origins (origin licensing) were laterally displaced (sliding) along the rDNA, away from a well-positioned nucleosome on one side. The authors' major hypothesis throughout this work is that the new MCM location(s) are intrinsically more efficient configurations for origin firing. The authors identify a chromatin remodeling enzyme, FUN30, whose deletion appears to suppress the earlier activation of rDNA origins in sir2∆ cells. Indeed, it appears that the reduction of rDNA origin activity in sir2∆ fun30∆ cells is severe enough to results in a substantial reduction in the rDNA array repeat length (number of repeats); the reduced rDNA length presumably facilitates it's more stable replication and maintenance.

Analysis of replication by 2D gels is marginally convincing, using 2D gels for this purpose is very challenging and tricky to quantify. The more quantitative analysis by EdU incorporation is more convincing of the suppression of the earlier replication caused by SIR2 deletion.

To address the mechanism of suppression, they analyze MCM positioning using ChEC, which in G1 cells shows partial displacement of MCM from normal position A to positions B and C in sir2∆ cells and similar but more complete displacement away from A to positions B and C in sir2fun30 cells. During S-phase in the presence of hydroxyurea, which slows replication progression considerably (and blocks later origin firing) MCM signals redistribute, which is interpreted to represent origin firing and bidirectional movement of MCMs (only one direction is shown), some of which accumulate near the replication fork barrier, consistent with their interpretation. They observe that MCMs displaced (in G1) to sites B or C in sir2∆ cells, disappear more rapidly during S-phase, whereas the similar dynamic is not observed in sir2∆fun30∆. This is the main basis for their conclusion that the B and C sites are more permissive than A. While this may be the simplest interpretation, there are limitations with this assay that undermine a rigorous conclusion (additional points below). The main problem is that we know the MCM complexes are mobile so disappearance may reflect displacement by other means including transcription which is high is the sir2∆ background. Indeed, the double mutant has greater level of transcription per repeat unit which might explain more displaced from A in G1. Thus, displacement might not always represent origin firing. Because the sir2 background profoundly changes transcription, and the double mutant has a much smaller array length associated with higher transcription, how can we rule out greater accessibility at site A, for example in sir2∆, leading to more firing, which is suppressed in sir2 fun30 due to greater MCM displacement away from A?

I think the critical missing data to solidly support their conclusions is a definitive determination of the site(s) of initiation using a more direct method, such as strand specific sequencing of EdU or nascent strand analysis. More direct comparisons of the strains with lower copy number to rule out this facet. As discussed in detail below, copy number reduction is known to suppress at least part of the sir2∆ effect so this looms over the interpretations. I think they are probably correct in their overall model based on the simplest interpretation of the data but I think it remains to be rigorously established. I think they should soften their conclusions in this respect.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors follow up on their previous work showing that in the absence of the Sir2 deacetylase the MCM replicative helicase at the rDNA spacer region is repositioned to a region of low nucleosome occupancy. Here they show that the repositioned displaced MCMs have increased firing propensity relative to non-displaced MCMs. In addition, they show that activation of the repositioned MCMs and low nucleosome occupancy in the adjacent region depend on the chromatin remodeling activity of Fun30.

Strengths:

The paper provides new information on the role of a conserved chromatin remodeling protein in the regulation of origin firing and in addition provides evidence that not all loaded MCMs fire and that origin firing is regulated at a step downstream of MCM loading.

Weaknesses:

The relationship between the author's results and prior work on the role of Sir2 (and Fob1) in regulation of rDNA recombination and copy number maintenance is not explored, making it difficult to place the results in a broader context. Sir2 has previously been shown to be recruited by Fob1, which is also required for DSB formation and recombination-mediated changes in rDNA copy number. Are the changes that the authors observe specifically in fun30 sir2 cells related to this pathway? Is Fob1 required for the reduced rDNA copy number in fun30 sir2 double mutant cells? 

Strains lacking SIR2 have unstable rDNA size, and FOB1 deletion stabilizes rDNA size in sir2 background. Likewise, FOB1 deletion influences the kinetics  rDNA size reduction in sir2 fun30 cells. However, the main effect of Fun30 in sir2 cells we were interested in, suppression of rDNA replication, is preserved in fob1 background, arguing that the observed effect is independent of Fob1 (see figure below). Given that the main focus of the paper is regulation of rDNA origins activity and that these changes were independent of Fob1, we had elected not to include these results in the original manuscript but will gladly include them in the revision.

Besides refuting the possible role of Fob1 in the FUN30-mediated activation of rDNA origin firing in sir2 cells, the use of fob1 background enabled us compare the activation of rDNA origins in the sir2 and sir2 fun30 strains with equally short rDNA size. The 2-D gels demonstrate a dramatic suppression of rDNA origin activity upon deletion of FUN30 in the sir2 fob1 strains with 35 rDNA copies.

Author response image 1.

The deletion of FUN30 diminishes the replication bubble signal in a fob1 sir2 strain with 35 rDNA copies by more than tenfold. The single rARS signal, marked with the arrow, originates from the rightmost rDNA repeat. This specific rightmost rDNA NheI fragment is approximately 25 kb in size, distinctly larger than the 4.7 kb NheI 1N rARS-containing fragments that originate from the internal rDNA repeats.

Reviewer #3 (Public Review):

Summary:

Heterochromatin is characterized by low transcription activity and late replication timing, both dependent on the NAD-dependent protein deacetylase Sir2, the founding member of the sirtuins. This manuscript addresses the mechanism by which Sir2 delays replication timing at the rDNA in budding yeast. Previous work from the same laboratory (Foss et al. PLoS Genetics 15, e1008138) showed that Sir2 represses transcription-dependent displacement of the Mcm helicase in the rDNA. In this manuscript, the authors show convincingly that the repositioned Mcms fire earlier and that this early firing partly depends on the ATPase activity of the nucleosome remodeler Fun30. Using read-depth analysis of sorted G1/S cells, fun30 was the only chromatin remodeler mutant that somewhat delayed replication timing in sir2 mutants, while nhp10, chd1, isw1, htl1, swr1, isw2, and irc5 had not effect. The conclusion was corroborated with orthogonal assays including two-dimensional gel electrophoresis and analysis of EdU incorporation at early origins. Using an insightful analysis with an Mcm-MNase fusion (Mcm-ChEC), the authors show that the repositioned Mcms in sir2 mutants fire earlier than the Mcm at the normal position in wild type. This early firing at the repositioned Mcms is partially suppressed by Fun30. In addition, the authors show Fun30 affects nucleosome occupancy at the sites of the repositioned Mcm, providing a plausible mechanism for the effect of Fun30 on Mcm firing at that position. However, the results from the MNAse-seq and ChEC-seq assays are not fully congruent for the fun30 single mutant. Overall, the results support the conclusions providing a much better mechanistic understanding how Sir2 affects replication timing at rDNA.

The reason that the results for the fun30 single mutant appear incongruent, with a larger signal of the +2 nucleosome in the MNase-seq plot but a negligible signal in the ChEC-seq plot is the paucity of displaced Mcm in the fun30 single mutant. Given the relative absence of displaced MCMs, the MCM-MNase fusion protein can't "light up" the +2 nucleosome.  We will comment on this in the revision to clarify this. 

Strengths

(1) The data clearly show that the repositioned Mcm helicase fires earlier than the Mcm in the wild type position.

(2) The study identifies a specific role for Fun30 in replication timing and an effect on nucleosome occupancy around the newly positioned Mcm helicase in sir2 cells.

Weaknesses

(1) It is unclear which strains were used in each experiment.

(2) The relevance of the fun30 phospho-site mutant (S20AS28A) is unclear.

(3) For some experiments (Figs. 3, 4, 6) it is unclear whether the data are reproducible and the differences significant. Information about the number of independent experiments and quantitation is lacking. This affects the interpretation, as fun30 seems to affect the +3 nucleosome much more than let on in the description.

We appreciate the reviewer pointing out places in which our manuscript omitted key pieces of information (items 1 and 3), and we will fix these oversights in our revision. 

With regard to point 2, we had written: 

“Fun30 is also known to play a role in the DNA damage response; specifically, phosphorylation of Fun30 on S20 and S28 by CDK1 targets Fun30 to sites of DNA damage, where it promotes DNA resection (Chen et al. 2016; Bantele et al. 2017). To determine whether the replication phenotype that we observed might be a consequence of Fun30's role in the DNA damage response, we tested non-phosphorylatable mutants for the ability to suppress early replication of the rDNA in sir2; these mutations had no effect on the replication phenotype (Figure 2B), arguing against a primary role for Fun30

in DNA damage repair that somehow manifests itself in replication.”

We will expand on this to clarify our point in the revision.

Author response:

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

eLife assessment

The authors report that optogenetic inhibition of hippocampal axon terminals in retrosplenial cortex impairs the performance of a delayed non-match to place task. The significance of findings elucidating the role of hippocampal projections to the retrosplenial cortex in memory and decision-making behaviors is important. However, the strength of evidence for the paper's claims is currently incomplete.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This is a study on the role of the retrosplenial cortex (RSC) and the hippocampus in working memory. Working memory is a critical cognitive function that allows temporary retention of information for task execution. The RSC, which is functionally and anatomically connected to both primary sensory (especially visual) and higher cognitive areas, plays a key role in integrating spatial-temporal context and in goal-directed behaviors. However, the specific contributions of the RSC and the hippocampus in working memory-guided behaviors are not fully understood due to a lack of studies that experimentally disrupt the connection between these two regions during such behaviors.

In this study, researchers employed eArch3.0 to silence hippocampal axon terminals in the RSC, aiming to explore the roles of these brain regions in working memory. Experiments were conducted where animals with silenced hippocampal axon terminals in the RSC performed a delayed non-match to place (DNMP) task. The results indicated that this manipulation impaired memory retrieval, leading to decreased performance and quicker decision-making in the animals. Notably, the authors observed that the effects of this impairment persisted beyond the light-activation period of the opsin, affecting up to three subsequent trials. They suggest that disrupting the hippocampal-RSC connection has a significant and lasting impact on working memory performance.

Strengths:

They conducted a study exploring the impact of direct hippocampal inputs into the RSC, a region involved in encoding spatial-temporal context and transferring contextual information, on spatial working memory tasks. Utilizing eArch3.0 expressed in hippocampal neurons via the viral vector AAV5-hSyn1-eArch3.0, they aimed to bilaterally silence hippocampal terminals located at the RSC in rats pre-trained in a DNMP task. They discovered that silencing hippocampal terminals in the RSC significantly decreased working memory performance in eArch+ animals, especially during task interleaving sessions (TI) that alternated between trials with and without light delivery. This effect persisted even in non-illuminated trials, indicating a lasting impact beyond the periods of direct manipulation. Additionally, they observed a decreased likelihood of correct responses following TI trials and an increased error rate in eArch+ animals, even after incorrect responses, suggesting an impairment in error-corrective behavior. This contrasted with baseline sessions where no light was delivered, and both eArch+ and control animals showed low error rates.

Weaknesses:

While I agree with the authors that the role of hippocampal inputs to the RSC in spatial working memory is understudied and merits further investigation, I find that the optogenetic experiment, a core part of this manuscript that includes viral injections, could be improved. The effects were rather subtle, rendering some of the results barely significant and possibly too weak to support major conclusions.

We thank Reviewer#1 for carefully and critically reading our manuscript, and for the valuable comments provided. The judged “subtlety” of the effects stems from a perspective according to which a quantitatively lower effect bears less biological significance for cognition. We disagree with this perspective and find it rather reductive for several reasons.

Once seen in the context of the animal’s ecology, subtle impairments can be life-threatening precisely because of their subtlety, leading the animal to confidently rely on a defective capacity, for such events as remembering the habitual location of a predator, or food source.

Also, studies in animal cognition often undertake complete, rather than graded, suppression of a given mechanism (in the same sense as that of “knocking out” a gene that is relevant for behaviour), leading to a gravelly, rather that gradually, impaired model system, to the point of not allowing a hypothetical causal link to be mechanistically revealed beyond its mere presence. This often hinders a thorough interpretation of the perturbed factor’s role. If a caricatural analogy is allowed, it would be as if we were to study the role of an animal’s legs by chopping them both off and observing the resulting behaviour.

In our study we conclude that silencing HIPP inputs in RSC perturbs cognition enough to impair behaviour while not disabling the animal entirely, as such allowing for behaviour to proceed, and for our observation of graded, decreased (not absent), proficiency under optogenetic silencing. So rather than weak, we would say the results are statistically significant, and biologically realistic.

Additionally, no mechanistic investigation was conducted beyond referencing previous reports to interpret the core behavioral phenotypes.

We fully agree with this being a weakness, as we wish we could have done more mechanistic studies to find out exactly what is Arch activation doing to HIPP-RSC transmission, which neurons are being affected, and perhaps in the future dissect its circuit determinants. We have all these goals very present and hope we can address them soon.

Reviewer #2 (Public Review):

The authors examine the impact of optogenetic inhibition of hippocampal axon terminals in the retrosplenial cortex (RSP) during the performance of a working memory T-maze task. Performance on a delayed non-match-to-place task was impaired by such inhibition. The authors also report that inhibition is associated with faster decision-making and that the effects of inhibition can be observed over several subsequent trials. The work seems reasonably well done and the role of hippocampal projections to retrosplenial cortex in memory and decision-making is very relevant to multiple fields. However, the work should be expanded in several ways before one can make firm conclusions on the role of this projection in memory and behavior.

We thank Reviewer#2 for carefully and critically reading our manuscript, and for the valuable comments provided.

(1) The work is very singular in its message and the experimentation. Further, the impact of the inhibition on behaviour is very moderate. In this sense, the results do not support the conclusion that the hippocampal projection to retrosplenial cortex is key to working memory in a navigational setting.

As we have mentioned in response to Reviewer#1, the judged “very moderate” effect stems from a perspective according to which a quantitatively lower effect bears less biological significance for cognition, precluding its consideration as “key” for behaviour. We disagree with this perspective and find it rather reductive for several reasons. Once seen in the context of the animal’s ecology, quantitatively lower impairments in working memory are no less key for this cognitive capacity, and can be life-threatening precisely because of their subtlety, leading the animal to confidently rely on a defective capacity, for such events as remembering the habitual location of a predator, or food source. Furthermore, studies in animal cognition often undertake complete, rather than graded, suppression of a given mechanism (in the same sense as “knocking out” a gene that is relevant for behaviour), leading to a gravelly, rather that gradually, impaired model system, to the point of not allowing a hypothetical causal link to be mechanistically revealed beyond its mere presence. This often hinders a thorough interpretation of its role.

In our study we conclude that silencing HIPP inputs in RSC perturbs behaviour enough to impair behaviour while not disabling the animal entirely, as such allowing for behaviour to proceed, and our observation of graded, decreased (not absent), proficiency under optogenetic silencing. So rather than weak, we would say the results are statistically significant, and biologically realistic.

(2) There are no experiments examining other types of behavior or working memory. Given that the animals used in the studies could be put through a large number of different tasks, this is surprising. There is no control navigational task. There is no working memory test that is non-spatial. Such results should be presented in order to put the main finding in context.

It is hard to gainsay this point. The more thorough and complete a behavioural characterization is, the more informative is the study, from every angle you look at it. While we agree that other forms of WM would be quite interesting in this context, we also cannot ignore the fact that DNMP is widely tested as a WM task, one that is biologically plausible, sensitive to perturbations of neural circuitry know to be at play therein, and fully accepted in the field. Faced with the impossibility of running further studies, for lack of additional funding and human resources, we chose to run this task.

A control navigational task would, in our understanding, be used to assess whether silencing HIPP projections to RSC would affect (spatial?) navigation, rather than WM, thus explaining the observed impairment. To this we have the following to say: Spatial Navigation is a very basic cognitive function, one that relies on body orientation relative to spatial context, on keeping an updated representation of such spatial context, (“alas”, as memory), and on guiding behaviour according to acquired knowledge about spatial context. Some of these functions are integral to spatial working memory, as such, they might indeed be affected.

Dissecting the determinants of spatial WM is indeed an ongoing effort, one that was not the intention of the current study, but also one that we have very present, in hope we can address in the future.

A non-spatial WM task would indeed vastly solidify our claims beyond spatial WM, onto WM. We have, for this reason, changed the title of the manuscript which now reads “spatial working memory”.

(3) The actual impact of the inhibition on activity in RSP is not provided. While this may not be strictly necessary, it is relevant that the hippocampal projection to RSP includes, and is perhaps dominated by inhibitory inputs. I wonder why the authors chose to manipulate hippocampal inputs to RSP when the subiculum stands as a much stronger source of afferents to RSP and has been shown to exhibit spatial and directional tuning of activity. The points here are that we cannot be sure what the manipulation is really accomplishing in terms of inhibiting RSP activity (perhaps this explains the moderate impact on behavior) and that the effect of inhibiting hippocampal inputs is not an effective means by which to study how RSP is responsive to inputs that reflect environmental locations.

We fully agree that neural recordings addressing the effect of silencing on RSC neural activity is relevant. We do wish we could have provided more mechanistic studies, to find out exactly what is Arch activation doing to HIPP-RSC transmission, which neurons are being affected, and thus dissecting its circuit determinants. We have all these goals very present and hope we can address them soon. Subiculum, which we mention in the Introduction, is indeed a key player in this complex circuitry, one whose hypothetical influence is the subject of experimental studies which will certainly reveal many other key elements.

(4) The impact of inhibition on trials subsequent to the trial during which optical stimulation was actually supplied seems trivial. The authors themselves point to evidence that activation of the hyperpolarizing proton pump is rather long-lasting in its action. Further, each sample-test trial pairing is independent of the prior or subsequent trials. This finding is presented as a major finding of the work, but would normally be relegated to supplemental data as an expected outcome given the dynamics of the pump when activated.

We disagree that this finding is “trivial”, and object to the considerations of “normalcy”, which we are left wondering about.

In lack of neurophysiological experiments (for the reasons stated above) to address this interesting finding, we chose to interpret it in light of (the few) published observations, such being the logical course of action in scientific reporting, given the present circumstances.

Evidence for such a prolonged effect in the context of behaviour is scarce (to our knowledge only the one we cite in the manuscript). As such, it is highly relevant to report it, and give it the relevance we do in our manuscript, rather than “relegating it to supplementary data”, as the reviewer considers being “normal”.

In the DNMP task the consecutive sample-test pairs are explicitly not independent, as they are part of the same behavioural session. This is illustrated by the simple phenomenon of learning, namely the intra-session learning curves, and the well-known behavioral trial-history effects. The brain does not simply erase such information during the ITI.

(5) In the middle of the first paragraph of the discussion, the authors make reference to work showing RSP responses to "contextual information in egocentric and allocentric reference frames". The citations here are clearly deficient. How is the Nitzan 2020 paper at all relevant here?

Nitzan 2020 reports the propagation of information from HIPP to CTX via SUB and RSC, thus providing a conduit for mnemonic information between the two structures, alternative to the one we target, thus providing thorough information concerning the HIPP-RSC circuitry at play during behaviour.

Alexander and Nitz 2015 precisely cite the encoding, and conjunction, of two types of contextual information, internal (ego-) and external (allocentric).

The subsequent reference is indeed superfluous here.

We thank the Reviewer#2 for calling our attention to the fact that references for this information are inadequate and lacking. We have now cited (Gill et al., 2011; Miller et al., 2019; Vedder et al., 2017) and refer readers to the review (Alexander et al., 2023)  for the purpose of illustrating the encoding of information in the two reference frames. In addition, we have substantially edited the Introduction and Discussion sections, and suppressed unnecessary passages.

(6) The manuscript is deficient in referencing and discussing data from the Smith laboratory that is similar. The discussion reads mainly like a repeat of the results section.

Please see above. We thank Reviewer#2 for this comment, we have now re-written the Discussion such that it is less of a summary of the Results and more focused on their implications and future directions.

Response to recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major

Line 101: Even with the tapered lambda fibre optic stub, if the fibre optics were longitudinally staggered by 2 millimetres, they would deliver light to diagonal regions in the horizontal plane rather than covering the full length of the RSC. Is this staggering pattern randomized or fixed? Additionally, Figure 1C is a bit misleading, as the light distribution pattern from the tapered fibre optic is likely to be more concentrated near the surface of the fibre, rather than spreading widely in a large spherical pattern.

The staggering is fixed. The elliptical (not spherical) contour in Fig 1C is not meant to convey any quantitative information, but rather to visually orient the reader towards the directions into which light will likely propagate, the effects of which we do not attempt to estimate here. We have made this contour smaller.

Line 119: The authors demonstrate the viral expression pattern of a representative animal and the overall expression patterns of all other animals in Figure 1 and the Supplementary Figures. However, numerous cases in the Supplementary Figures exhibit viral leakages and strong expressions in adjacent cortical and thalamic areas. Although there is a magnified view of the RSC's expression pattern in Figure 1, authors should show the same way in the supplemental data as well. Additionally, the degree of viral expression in the hippocampal subregions varies substantially across animals. This variation is concerning and impacts the interpretation of the results.

The viral construct was injected in the HIPP at coordinates based on our previous work (Ferreira-Fernandes et al., 2019) wherein injections of a similar vector in mid-dorsal HIPP resulted in widespread expression throughout the medial mesocortex AP extent, RSC through CG, as well as other areas in which HIPP establishes synapses. These were studied in detail then, by estimating the density of axon terminals. In the present work we did not acquire high-mag images of all slices, since they were too expensive, and we had this information from the study above. Still, we have now added further examples of high-mag images taken from eArch and CTRL animals.

We believe it is important here to mention the fact that the virus we use, AAV5, only travels anterograde and is static (i.e. it does not travel transynaptically).

Variations in viral expression are to be expected even if injections happen in the exact same way. It is crucial then, that fibre positioning is constant across animals, to guarantee that its relationship with viral expression is thence consistent, and to render irrelevant whatever off-target expression of the viral construct. We have ascertained this condition post-mortem in all our animals.

Line 124: Another point regarding the viral expressions and optical fibre implants used to inhibit the HIPP-RSC pathway is that the RSC and HIPP extend substantially along the anterior-posterior axis. The authors should demonstrate how the viral expression is distributed along this axis and indicate where the tip of the tapered optical fibre ended by marking it in the histological images. This information is crucial to confirm the authors' claim that the hippocampal projection terminals were indeed modulated by optical light. Also, the manuscript would benefit from details about the power/duration and/or modulation of the light used.

In both Figures 1 and S1 panels we can clearly see the tracks formed by the fibres. This provides examples of such dual angle placement vis a vis the expression of the construct, demonstrating that the former is fully targeted towards the latter. We have added markers to highlight these tracks and an example of a “full” track in figure S1. We did not have animals deviating from this relative positioning to any significant extent. The methods section mentions illumination power as 240mA, and we have now added estimated illumination time as well.

Line 141: The authors should include data on task performance during learning and baseline sessions for each animal, to demonstrate that they fully grasped the task rules and that achieving a 75% performance ratio was sufficient.

DNMP is a standard WM task used for many decades, in which animals reach performances above 75% in 4-8 sessions. We have used it extensively, and never saw any deviations from this learning rate and curve. We ran daily sessions until animals reached 75%, and thereafter until they maintained this performance, or above, for three consecutive sessions (the data points we show). We saw no deviations from what is published, nor from what is our own extensive experience, and thence are fully confident that all animals included in this manuscript grasped task rules.

Line 146: While the study focused on inhibiting inputs during the test run (retrieval phase), it would be beneficial to also inhibit inputs during the sample run (encoding phase) and the delay period. This would help confirm whether the silencing affects only working memory retrieval, or if it also impacts encoding and maintenance.

We agree, it would be very interesting to determine if there are any effects of silencing HIPP RSC terminals during Sample. However, since there is a limit to the number of trials per session, and to the total number of sessions, we could not run the three manipulations within each session of our experimental design, as that would lower the number of trials per condition to an extent that would affect statistical power. Silencing HIPP RSC terminals during Sample would best be a separate experiment, asking a different question, and perhaps within an experimental design distinct from the one envisioned.

A very important point here relates to the fact that the effects of optogenetic manipulation do not limit themselves to the illumination epoch, in fact they extend far beyond onto the 3rd trial post-illumination. The insertion of Sample-illuminated trials interleaved in the same session would fundamentally affect the interpretation of experimental results, as we could not attribute lower performances to the effects in either or both manipulated epochs.

Line 225: Figure 5 illustrates that silencing the inputs results in an extended impairment of working memory performance. However, it's unclear if there are any behavioural changes during the sample run. The inhibition could potentially affect encoding in the subsequent sample run, considering the inter-trial interval (ITI) is only 20 seconds.

From the observation of behaviour and the analysis of our data, we saw no overt “behavioural changes during the sample run”, as latencies and speeds were essentially unchanged.

If what is meant by your comment is the effect of optogenetic manipulation being protracted from the Test towards the Sample epoch, we find this unlikely. Conservatively, we estimate the peak of our optogenetic manipulation to occur around the time light is delivered, the Test phase, rather than 20-30 secs later.

In theory, any effect of optogenetic silencing of HIPP terminals in RSC can cause disturbances in encoding or Sample, the ITI itself, and the epoch in which mnemonic information retrieved from the Sample epoch is confronted with the contextual information present during Test, leading to a decision. This is regardless of the illumination epoch, and even if the effect of optogenetic manipulation is not prolonged in time. 

Since in our experiments we specifically target the Test epoch, and there is, in all likelihood, a decaying magnitude of neurophysiological effects, manifest in the reported decaying nature of the manipulation mechanism, and in our observed decrease of behavioural proficiency from subsequent trials 1:4, we are convinced that a conservative interpretation is that our major effect is concentrated in the epoch in which we deliver light - the Test epoch, the consequences of which (possibly related to short term plasticity events taking place within the HIPP-RSC neural circuit) extending further in time.

Line 410: The methods section on the surgical procedure could be clearer, particularly regarding the coordinates for microinjection and fibre implantation. A more precise description would aid reader comprehension.

The now-reported injection and implantation coordinates include the numbers corresponding to the distances, in mm, from Bregma to the targets, in the three stereotaxic dimensions considered: antero-posterior, medial-lateral left and right, and dorso-ventral, as well as the angle at which the fibres were positioned. We have added labels to the figures to highlight the fibreoptic track locations. We will be happy to provide further details as deemed necessary.

Line 461: It would be helpful to know if each animal displayed a preference for the left or right side. Including a description or figure showing that the performance ratio exceeded 75% in both left and right trials would provide a more comprehensive understanding of the animals' behaviour.

In the DNMP, an extensively used and documented WM task, it is an absolute pre-condition that no animals are biased to either side. As such, we did not use any animal that showed such bias.<br /> We have not observed this to be the case in any of our candidate animals, nor would we use any animal exhibiting such a preference.

Minor

Line 25: In the INTRODUCTION section, the authors introduce ego-centric and allocentric variables in the RSC. However, if they intend to discuss this feature, there is no supporting data for ego-centric or allocentric variables in the Results section.

We agree. The extent of the discussion of ego vs allo-centric variables in our manuscript might venture a bit out of the main subject. It was included to provide wider context to our reporting of the data, considering that spatial working memory is indeed one instance in which egocentric- and allocentric-referenced cognitive mechanisms confront each other, and one in which silencing the HIPP input to a cortical region thence involved would likely disturb ensuing computations. We have now substantially edited the manuscript’s Introduction and Discussion, sections, namely toning down this aspect.

Line 125: In the section title, DNMT -> DNMP obviously.

We have corrected this passage.

Figures: The quality of the figure panels does not meet the expected standards. For example, scale bars are missing in many panels (e.g., Figure 1A bottom, 1B, 1C, S1), figure labels are misaligned (as seen in Figure 3A-B compared to 3C, same with Figure 5), and there is inconsistency in color schemes (e.g., Figure 3C versus Figure 6, where 'Error' versus 'Correct' is depicted using green versus blue, respectively).

We have now corrected these inconsistencies and mistakes.

Author response:

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

eLife assessment

This study presents an important finding on the influence of visual uncertainty and Bayesian cue combination on implicit motor adaptation in young healthy participants, hereby linking perception and action during implicit adaptation. The evidence supporting the claims of the authors is convincing. The normative approach of the proposed PEA model, which combines ideas from separate lines of research, including vision research and motor learning, opens avenues for future developments. This work will be of interest to researchers in sensory cue integration and motor learning.

Thank you for the updated assessment. We are also grateful for the insightful and constructive comments from the reviewers, which have helped us improve the manuscript again. We made necessary changes following their comments (trimmed tests, new analysis results, etc) and responded to the comments in a point-by-point fashion below. We hope to publish these responses alongside the public review. Thank you again for fostering the fruitful discussion here.

Public Reviews:

Reviewer #1 (Public Review):

I appreciate the normative approach of the PEA model and am eager to examine this model in the future. However, two minor issues remain:

(1) Clarification on the PReMo Model:

The authors state, "The PReMo model proposes that this drift comprises two phases: initial proprioceptive recalibration and subsequent visual recalibration." This description could misinterpret the intent of PReMo. According to PReMo, the time course of the reported hand position is merely a read-out of the *perceived hand position* (x_hat in your paper). Early in adaptation, the perceived hand position is biased by the visual cursor (x_hat in the direction of the cursor); towards the end, due to implicit adaptation, x_hat reduces to zero. This is the same as PEA. I recommend that the authors clarify PReMo's intent to avoid confusion.

Note, however, the observed overshoot of 1 degree in the reported hand position. In the PReMo paper, we hypothesized that this effect is due to the recalibration of the perceived visual target location (inspired by studies showing that vision is also recalibrated by proprioception, but in the opposite direction). If the goal of implicit adaptation is to align the perceived hand position (x_hat) with the perceived target position (t_hat), then there would be an overshoot of x_hat over the actual target position.

PEA posits a different account for the overshoot. It currently suggests that the reported hand position combines x_hat (which takes x_p as input) with x_p itself. What is reasoning underlying the *double occurrence* of x_p?

There seem to be three alternatives that seem more plausible (and could lead to the same overshooting): 1) increasing x_p's contribution (assuming visual uncertainty increases when the visual cursor is absent during the hand report phase), 2) decreasing sigma_p (assuming that participants pay more attention to the hand during the report phase), 3) it could be that the perceived target position undergoes recalibration in the opposite direction to proprioceptive recalibration. All these options, at least to me, seem equally plausible and testable in the future.

For clarification of the PReMo model’s take on Fig4A, we now write:

“The PReMo model proposes that the initial negative drift reflects a misperceived hand location, which gradually reduces to zero, and the late positive drift reflects the influence of visual calibration of the target (Tsay, Kim, Saxena, et al., 2022). ”

However, we would like to point out that the PEA model does not predict a zero (perceived hand location) even at the late phase of adaptation: it remains negative, though not as large as during initial adaptation (see Figure 4A, red line). Furthermore, we have not seen any plausible way to use a visually biased target to explain the overshoot of the judged hand location (see below when we address the three alternative hypotheses the reviewer raised).

We don’t think the “double” use of xp is a problem, simply because there are TWO tasks under investigation when the proprioceptive changes are measured along with adaptation. The first is the reaching adaptation task itself: moving under the influence of the clamped cursor. This task is accompanied by a covert estimation of hand location after the movement (). Given the robustness of implicit adaptation, this estimation appears mandatory and automatic. The second task is the hand localization task, during which the subject is explicitly asked to judge where the hand is. Here, the perceived hand is based on the two available cues, one is the actual hand location xp, and the other is the influence from the just finished reaching movement (i.e., ). For Bayesian modeling from a normative perspective, sensory integration is based on the available cues to fulfill the task. For the second task of reporting the hand location, the two cues are xp and (with a possible effect of the visual target, which is unbiased since it is defined as 0 in model simulation; thus, its presence does not induce any shift effect). xp is used sequentially in this sense. Thus, its dual use is well justified.

Our hypothesis is that the reported hand position results from a combination of from the previous movement and the current hand position xp. However, specifically for the overshoot of the judged hand location in the late part of the adaptation (Fig4A), the reviewer raised three alternative explanations by assuming that the PReMo model is correct. Under the PReMo model, the estimated hand location is only determined by , and xp is not used in the hand location report phase. In addition, (with xp used once) and a visual recalibration of the target can explain away the gradual shift from negative to positive (overshoot).

We don’t think any of them can parsimoniously explain our findings here, and we go through these three hypotheses one by one:

(1) increasing xp's contribution (assuming visual uncertainty increases when the visual cursor is absent during the hand report phase)

(2) decreasing σp (assuming that participants pay more attention to the hand during the report phase)

The first two alternative explanations basically assume that xp has a larger contribution (weighting in Bayesian terms) in the hand location report phase than in the adaptation movement phase, no matter due to an increase in visual uncertainty (alternative explanation 1) or a reduction in proprioceptive uncertainty (alternative explanation 2). Thus, we assume that the reviewer suggests that a larger weight for xp can explain why the perceived hand location changes gradually from negative to positive. However, per the PReMo model, a larger weight for the xp will only affect , which is already assumed to change from negative to zero. More weight in  in the hand report phase (compared to the adaptation movement phase) would not explain away the reported hand location from negative to positive. This is because no matter how much weight the xp has, the PReMo model assumes a saturation for the influence of xp on . Thus would not exceed zero in the late adaptation. Then, the PReMo model would rely on the so-called visual shift of the target to explain the overshoot. This leads us to the third alternative the reviewer raised:

(3) it could be that the perceived target position undergoes recalibration in the opposite direction to proprioceptive recalibration.

The PReMo model originally assumed that the perceived target location was biased in order to explain away the positive overshoot of the reported hand location. We assume that the reviewer suggests that the perceived target position, which is shifted to the positive direction, also “biases” the perceived hand position. We also assume that the reviewer suggests that the perceived hand location after a clamp trial () is zero, and somehow the shifted perceived target position “biases” the reported hand location after a clamp trial. Unfortunately, we did not see any mathematical formulation of this biasing effect in the original paper (Tsay, Kim, Haith, et al., 2022). We are not able to come up with any formulation of this hypothesized biasing effect based on Bayesian cue integration principles. Target and hand are two separate perceived items; how one relates to another needs justification from a normative perspective when discussing Bayesian models. Note this is not a problem for our PEA models, in which both cues used are about hand localization, one is and the other is xp.

We believe that mathematically formulating the biasing effect (Figure 4A) is non-trivial since the reported hand location changes continuously from negative to positive. Thus, quantitative model predictions, like the ones our PEA model presents here, are needed.

To rigorously test the possible effect of visual recalibration of the target, there are two things to do: 1) use the psychometric method to measure the biased perception of the target, and 2) re-do Tsay et al. 2020 experiment without the target. For 2), compared to the case with the target, the PEA model would predict a larger overshoot, while the PReMo would predict a smaller overshoot or even zero overshoot. This can be left for future studies.

(2) Effect of Visual Uncertainty on Error Size:

I appreciate the authors' response about methodological differences between the cursor cloud used in previous studies and the Gaussian blob used in the current study. However, it is still not clear to me how the authors reconcile previous studies showing that visual uncertainty reduced implicit adaptation for small but not large errors (Tsay et al, 2021; Makino, et al 2023) with the current findings, where visual uncertainty reduced implicit adaptation for large but not small errors.

Could the authors connect the dots here: I could see that the cursor cloud increases potential overlap with the visual target when the visual error is small, resulting in intrinsic reward-like mechanisms (Kim et al, 2019), which could potentially explain attenuated implicit adaptation for small visual errors. However, why would implicit adaptation in response to large visual errors remain unaffected by the cursor cloud? Note that we did verify that sigma_v is increased in (Tsay et al. 2021), so it is unlikely due to the cloud simply failing as a manipulation of visual uncertainty.

In addition, we also reasoned that testing individuals with low vision could offer a different test of visual uncertainty (Tsay et al, 2023). The advantage here is that both control and patients with low vision are provided with the same visual input-a single cursor. Our findings suggest that uncertainty due to low vision also shows reduced implicit adaptation in response to small but not large errors, contrary to the findings in the current paper. Missing in the manuscript is a discussion related to why the authors' current findings contradict those of previous results.

For connecting the dots for two previous studies (Tsay et al., 2021, 2023); Note Makino et al., 2023 is not in this discussion since it investigated the weights of multiple cursors, as opposed to visual uncertainty associated with a cursor cloud):

First, we want to re-emphasize that using the cursor cloud to manipulate visual uncertainty brings some confounds, making it not ideal for studying visuomotor adaptation. For example, in the error clamp paradigm, the error is defined as angular deviation. The cursor cloud consists of multiple cursors spanning over a range of angles, which affects both the sensory uncertainty (the intended outcome) and the sensory estimate of angles (the error estimate, the undesired outcome). In Bayesian terms, the cursor cloud aims to modulate the sigma of a distribution (σv) in our model), but it additionally affects the mean of the distribution (µ). This unnecessary confound is neatly avoided by using cursor blurring, which is still a cursor with its center (µ) unchanged from a single cursor. Furthermore, as correctly pointed out in the original paper by Tsay et al., 2020, the cursor cloud often overlaps with the visual target; this "target hit" would affect adaptation, possibly via a reward learning mechanism (Kim et al., 2019). This is a second confound that accompanies the cursor cloud. Yes, the cursor cloud was verified as associated with high visual uncertainty (Tsay et al., 2021); this verification was done with a psychophysics method with a clean background, not in the context of a hand reaching a target that is needed. Thus, despite the cursor cloud having a sizeable visual uncertainty, our criticisms for it still hold when used in error-clamp adaptation.

Second, bearing these confounds of the cursor cloud in mind, we postulate one important factor that has not been considered in any models thus far that might underlie the lack of difference between the single-cursor clamp and the cloud-cursor clamp when the clamp size is large: the cursor cloud might be harder to ignore than a single cursor. For Bayesian sensory integration, the naive model is to consider the relative reliability of cues only. Yes, the cloud is more uncertain in terms of indicating the movement direction than a single cursor. However, given its large spread, it is probably harder to ignore during error-clamp movements. Note that ignoring the clamped cursor is the task instruction, but the large scatter of the cursor cloud is more salient and thus plausible and harder to ignore. This might increase the weighting of the visual cue despite its higher visual uncertainty. This extra confound is arguably minimized by using the blurred cursor as in our Exp4 since the blurred cursor did not increase the visual angle much (Figure 5D; blurred vs single cursor: 3.4mm vs 2.5mm in radius, 3.90o vs  2.87o in spread). In contrast, the visual angle of the dot cloud is at least a magnitude larger (cursor cloud vs. single cursor: at least 25o vs. 2.15o in the spread, given a 10o standard deviation of random sampling).

Third, for the low-vision study (Tsay et al., 2023), the patients indeed show reduced implicit adaptation for a 3 o clamp (consistent with our PEA model) but an intact adaptation for 30-degree clamp (not consistent). Though this pattern appears similar to what happens for normal people whose visual uncertainty is upregulated by cursor cloud (Tsay et al., 2021), we are not completely convinced that the same underlying mechanism governs these two datasets. Low-vision patients indeed have higher visual uncertainty about color, brightness, and object location, but their visual uncertainty about visual motion is still unknown. Due to the difference in impairment among low vision people (e.g., peripheral or central affected) and the different roles of peripheral and central vision in movement planning and control (Sivak & Mackenzie, 1992), it is unclear about the overall effect of visual uncertainty in low vision people. The direction of cursor movement that matters for visuomotor rotation here is likely related to visual motion perception. Unfortunately, the original study did not measure this uncertainty in low-vision patients. We believe our Exp1 offers a valid method for this purpose for future studies. More importantly, we should not expect low-vision patients to integrate visual cues in the same way as normal people, given their long-term adaptation to their vision difficulties. Thus, we are conservative about interpreting the seemingly similar findings across the two studies (Tsay et al., 2021, 2023) as revealing the same mechanism.

A side note: these two previous studies proposed a so-called mis-localization hypothesis, i.e., the cursor cloud was mislocated for small clamp size (given its overlapping with the target) but not for large clamp size. They suggested that the lack of uncertainty effect at small clamp sizes is due to mislocalization, while the lack of uncertainty effect at large clamp sizes is because implicit adaptation is not sensitive to uncertainty at large angles. Thus, these two studies admit that cursor cloud not only upregulates uncertainty but also generates an unwanted effect of so-called “mis-localization” (overlapping with the target). Interestingly, their hypothesis about less sensitivity to visual uncertainty for large clamps is not supported by a model or theory but merely a re-wording of the experiment results.

In sum, our current study cannot offer an easy answer to "connect the dots" in the aforementioned two studies due to methodology issues and the specialty of the population. However, for resolving conflicting findings, our study suggests solutions include using a psychometric test to quantify visual uncertainty for cursor motion (Exp1), a better uncertainty-manipulation method to avoid a couple of confounds (Exp4, blurred cursor), and a falsifiable model. Future endeavors can solve the difference between studies based on the new insights from the current.

Reviewer #2 (Public Review):

Summary:

The authors present the Perceptual Error Adaptation (PEA) model, a computational approach offering a unified explanation for behavioral results that are inconsistent with standard state-space models. Beginning with the conventional state-space framework, the paper introduces two innovative concepts. Firstly, errors are calculated based on the perceived hand position, determined through Bayesian integration of visual, proprioceptive, and predictive cues. Secondly, the model accounts for the eccentricity of vision, proposing that the uncertainty of cursor position increases with distance from the fixation point. This elegantly simple model, with minimal free parameters, effectively explains the observed plateau in motor adaptation under the implicit motor adaptation paradigm using the error-clamp method. Furthermore, the authors experimentally manipulate visual cursor uncertainty, a method established in visuomotor studies, to provide causal evidence. Their results show that the adaptation rate correlates with perturbation sizes and visual noise, uniquely explained by the PEA model and not by previous models. Therefore, the study convincingly demonstrates that implicit motor adaptation is a process of Bayesian cue integration

Strengths:

In the past decade, numerous perplexing results in visuomotor rotation tasks have questioned their underlying mechanisms. Prior models have individually addressed aspects like aiming strategies, motor adaptation plateaus, and sensory recalibration effects. However, a unified model encapsulating these phenomena with a simple computational principle was lacking. This paper addresses this gap with a robust Bayesian integration-based model. Its strength lies in two fundamental assumptions: motor adaptation's influence by visual eccentricity, a well-established vision science concept, and sensory estimation through Bayesian integration. By merging these well-founded principles, the authors elucidate previously incongruent and diverse results with an error-based update model. The incorporation of cursor feedback noise manipulation provides causal evidence for their model. The use of eye-tracking in their experimental design, and the analysis of adaptation studies based on estimated eccentricity, are particularly elegant. This paper makes a significant contribution to visuomotor learning research.

The authors discussed in the revised version that the proposed model can capture the general implicit motor learning process in addition to the visuomotor rotation task. In the discussion, they emphasize two main principles: the automatic tracking of effector position and the combination of movement cues using Bayesian integration. These principles are suggested as key to understanding and modeling various motor adaptations and skill learning. The proposed model could potentially become a basis for creating new computational models for skill acquisition, especially where current models fall short.

Weaknesses:

The proposed model is described as elegant. In this paper, the authors test the model within a limited example condition, demonstrating its relevance to the sensorimotor adaptation mechanisms of the human brain. However, the scope of the model's applicability remains unclear. It has shown the capacity to explain prior data, thereby surpassing previous models that rely on elementary mathematics. To solidify its credibility in the field, the authors must gather more supporting evidence.

Indeed, our model here is based on one particular experimental paradigm, i.e., the error-clamp adaptation. We used it simply because 1) this paradigm is one rare example that implicit motor learning can be isolated in a clean way, and 2) there are a few conflicting findings in the literature for us to explain away by using a unified model.

For our model’s broad impact, we believe that as long as people need to locate their effectors during motor learning, the general principle laid out here will be applicable. In other words, repetitive movements with a Bayesian cue combination of movement-related cues can underlie the implicit process of various motor learning. To showcase its broad impact, in upcoming studies, we will extend this model to other motor learning paradigms, starting from motor adaptation paradigms that involve both explicit and implicit processes.

Reviewer #3 (Public Review):

(2.1) Summary

In this paper, the authors model motor adaptation as a Bayesian process that combines visual uncertainty about the error feedback, uncertainty about proprioceptive sense of hand position, and uncertainty of predicted (=planned) hand movement with a learning and retention rate as used in state space models. The model is built with results from several experiments presented in the paper and is compared with the PReMo model (Tsay, Kim et al., 2022) as well as a cue combination model (Wei & Körding, 2009). The model and experiments demonstrate the role of visual uncertainty about error feedback in implicit adaptation.

In the introduction, the authors notice that implicit adaptation (as measured in error-clamp based paradigms) does not saturate at larger perturbations, but decreases again (e.g. Moorehead et al., 2017 shows no adaptation at 135{degree sign} and 175{degree sign} perturbations). They hypothesized that visual uncertainty about cursor position increases with larger perturbations since the cursor is further from the fixated target. This could decrease importance assigned to visual feedback which could explain lower asymptotes.

The authors characterize visual uncertainty for 3 rotation sizes in a first experiment, and while this experiment could be improved, it is probably sufficient for the current purposes. Then the authors present a second experiment where adaptation to 7 clamped errors are tested in different groups of participants. The models' visual uncertainty is set using a linear fit to the results from experiment 1, and the remaining 4 parameters are then fit to this second data set. The 4 parameters are 1) proprioceptive uncertainty, 2) uncertainty about the predicted hand position, 3) a learning rate and 4) a retention rate. The authors' Perceptual Error Adaptation model ("PEA") predicts asymptotic levels of implicit adaptation much better than both the PReMo model (Tsay, Kim et al., 2022), which predicts saturated asymptotes, or a causal inference model (Wei & Körding, 2007) which predicts no adaptation for larger rotations. In a third experiment, the authors test their model's predictions about proprioceptive recalibration, but unfortunately compare their data with an unsuitable other data set (Tsay et al. 2020, instead of Tsay et al. 2021). Finally, the authors conduct a fourth experiment where they put their model to the test. They measure implicit adaptation with increased visual uncertainty, by adding blur to the cursor, and the results are again better in line with their model (predicting overall lower adaptation), than with the PReMo model (predicting equal saturation but at larger perturbations) or a causal inference model (predicting equal peak adaptation, but shifted to larger rotations). In particular the model fits for experiment 2 and the results from experiment 4 show that the core idea of the model has merit: increased visual uncertainty about errors dampens implicit adaptation.

(2.2) Strengths

In this study the authors propose a Perceptual Error Adaptation model ("PEA") and the work combines various ideas from the field of cue combination, Bayesian methods and new data sets, collected in four experiments using various techniques that test very different components of the model. The central component of visual uncertainty is assessed in a first experiment. The model uses 4 other parameters to explain implicit adaptation. These parameters are: 1) a learning and 2) a retention rate, as used in popular state space models and the uncertainty (variance) of 3) predicted and 4) proprioceptive hand position. In particular, the authors observe that asymptotes for implicit learning do not saturate, as claimed before, but decrease again when rotations are very large and that this may have to do with visual uncertainty (e.g. Tsay et al., 2021, J Neurophysiol 125, 12-22). The final experiment confirms predictions of the fitted model about what happens when visual uncertainty is increased (overall decrease of adaptation). By incorporating visual uncertainty depending on retinal eccentricity, the predictions of the PEA model for very large perturbations are notably different from, and better than, the predictions of the two other models it is compared to. That is, the paper provides strong support for the idea that visual uncertainty of errors matters for implicit adaptation.

(2.3) Weaknesses

Although the authors don't say this, the "concave" function that shows that adaptation does not saturate for larger rotations has been shown before, including in papers cited in this manuscript.

For a proper citation of the “concave” adaptation function: we assume the reviewer is referring to the study by Morehead, 2017 which tested large clamp sizes up to 135 o and 175 o. Unsurprisingly, the 135 o and 175 o conditions lead to nearly zero adaptation, possibly due to the trivial fact that people cannot even see the moving cursor. We have quoted this seminar study from the very beginning. All other error-clamp studies with a block design emphasized an invariant or saturated implicit adaptation with large rotations (e.g., Kim, et al., 2019).

The first experiment, measuring visual uncertainty for several rotation sizes in error-clamped paradigms has several shortcomings, but these might not be so large as to invalidate the model or the findings in the rest of the manuscript. There are two main issues we highlight here. First, the data is not presented in units that allow comparison with vision science literature. Second, the 1 second delay between movement endpoint and disappearance of the cursor, and the presentation of the reference marker, may have led to substantial degradation of the visual memory of the cursor endpoint. That is, the experiment could be overestimating the visual uncertainty during implicit adaptation.

For the issues related to visual uncertainty measurement in Exp1:

First, our visual uncertainty is about cursor motion direction in the display plane, and the measurement in Exp1 has never been done before. Thus, we do not think our data is comparable to any findings in visual science about fovea/peripheral comparison. We quoted Klein and others’ work (Klein & Levi, 1987; Levi et al., 1987) in vision science since their studies showed that the deviation from the fixation is associated with an increase in visual uncertainty. Their study thus inspired us to conduct Exp1 to probe how our concerned visual uncertainty (specifically for visual motion direction) changes with an increasing deviation from the fixation. Any model and its model parameters should be specifically tailored to the task or context it tries to emulate. In our case, motion direction in a center-out-reaching setting is the modeled context, and all the relevant model parameters should be specified in movement angles. This is particularly important since we need to estimate parameters from one experiment to predict behaviors in another experiment.

Second, the 1s delay of the reference cursor has minimal impact on the estimate of visual uncertainty based on previous vision studies. Our Exp1 used a similar visual paradigm by (White et al., 1992), which shows that delay does not lead to an increase in visual uncertainty over a broad range of values (from 0.2s to >1s, see their Figure 5-6).

These two problems have been addressed in the revised manuscript, with proper citations listed.

The paper's third experiment relies to a large degree on reproducing patterns found in one particular paper, where the reported hand positions - as a measure of proprioceptive sense of hand position - are given and plotted relative to an ever present visual target, rather than relative to the actual hand position. That is, 1) since participants actively move to a visual target, the reported hand positions do not reflect proprioception, but mostly the remembered position of the target participants were trying to move to, and 2) if the reports are converted to a difference between the real and reported hand position (rather than the difference between the target and the report), those would be on the order of ~20° which is roughly two times larger than any previously reported proprioceptive recalibration, and an order of magnitude larger than what the authors themselves find (1-2°) and what their model predicts. Experiment 3 is perhaps not crucial to the paper, but it nicely provides support for the idea that proprioceptive recalibration can occur with error-clamped feedback.

Reviewer 3 thinks Tsay 2020 dataset is not appropriate for our theorization, but we respectfully disagree. For the three points raised here, we would like to elaborate:

(1) As we addressed in the previous response, the reported hand location in Figure 4A (Tsay et al., 2020) is not from a test of proprioceptive recalibration as conventionally defined. In the revision, we explicitly state that this dataset is not about proprioceptive recalibration and also delete texts that might mislead people to think so (see Results section). Instead, proprioceptive recalibration is measured by passive movement, as in our Exp3 (Figure 4E). For error-clamp adaptation here, "the remembered position of the target" is the target. Clearly, the participants did not report the target position, which is ever-present. Instead, their reported hand location shows an interestingly continuous change with ongoing adaptation.

(2) Since the Tsay 2020 dataset is not a so-called proprioceptive recalibration, we need not take the difference between the reported location and the actual hand location. Indeed, the difference would be ~20 degrees, but comparing it to the previously reported proprioceptive recalibration is like comparing apples to oranges. In fact, throughout the paper, we refer to the results in Fig 4A as “reported hand location”, not proprioceptive recalibration. The target direction is defined as zero degree thus its presence will not bias the reported hand in the Bayesian cue combination (as this visual cue has a mean value of 0). Using the target as the reference also simplifies our modeling.

(3) Exp3 is crucial for our study since it shows our model and its simple Bayesian cue combination principle are applicable not only to implicit adaptation but also to proprioceptive measures during adaptation. Furthermore, it reproduced the so-called proprioceptive recalibration and explained it away with the same Bayesian cue combination as the adaptation. We noticed that this field has accumulated an array of findings on proprioceptive changes induced by visuomotor adaptation. However, currently, there is a lack of a computational model to quantitatively explain them. Our study at least made an initial endeavor to model these changes.

Perhaps the largest caveat to the study is that it assumes that people do not look at the only error feedback available to them (and can explicitly suppress learning from it). This was probably true in the experiments used in the manuscript, but unlikely to be the case in most of the cited literature. Ignoring errors and suppressing adaptation would also be a disastrous strategy to use in the real world, such that our brains may not be very good at this. So the question remains to what degree - if any - the ideas behind the model generalize to experiments without fixation control, and more importantly, to real life situations.

The largest caveat raised by the reviewer appears to be directed to the error-clamp paradigm in general, not only to our particular study. In essence, this paradigm indeed requires participants to ignore the clamped error; thus, its induced adaptive response can be attributed to implicit adaptation. The original paper that proposed this paradigm (Morehead et al., 2017) has been cited 220 times (According to Google Scholar, at the time of this writing, 06/2024), indicating that the field has viewed this paradigm in a favorable way.

Furthermore, we agree that this kind of instruction and feedback (invariant clamp) differ from daily life experience, but it does not prevent us from gaining theoretical insights by studying human behaviors under this kind of "artificial" task setting. Thinking of the saccadic adaptation (Deubel, 1987; Kojima et al., 2004): jumping the target while the eye moves towards it, and this somewhat artificial manipulation again makes people adapt implicitly, and the adaptation itself is a "disastrous" strategy for real-life situations. However, scientists have gained an enormous understanding of motor adaptation using this seemingly counterproductive adaptation in real life. Also, think of perceptual learning of task-irrelevant stimuli (Seitz & Watanabe, 2005, 2009): when participants are required to learn to discriminate one type of visual stimuli, the background shows another type of stimuli, which people gradually learn even though they do not even notice its presence. This "implicit" learning can be detrimental to our real life, too, but the paradigm itself has advanced our understanding of the inner workings of the cognitive system.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

L101: There is a typo: (Tsay et al., 2020), 2020) should be corrected to (Tsay et al., 2020).

Thanks for pointing it out, we corrected this typo.

L224-228: It would be beneficial to evaluate the validity of the estimated sigma_u and sigma_p based on previous reports.

We can roughly estimate σu by evaluating the variability of reaching angles during the baseline phase when no perturbation is applied. The standard deviation of the reaching angle in Exp 2 is 5.128o±0.190o, which is close to the σu estimated by the model (5.048o). We also used a separate perceptual experiment to test the proprioceptive uncertainty (n = 13, See Figure S6), σp from this experiment is 9.737o±5.598o, also close to the σp extracted by the model (11.119o). We added these new analysis results to the final version of the paper.

L289-298: I found it difficult to understand the update equations of the proprioceptive calibration based on the PEA model. Providing references to the equations or better explanations would be helpful.

We expanded the process of proprioceptive calibration in Supplementary Text 1 with step-by-step equations and more explanations. 

Reviewer #3 (Recommendations For The Authors):

Suggestions (or clarification of previous suggestions) for revisions

The authors persist on using the Tsay et al 2020 paper despite its many drawbacks which the authors attempt to address in their reply. But the main drawback is that the results in the 2020 paper is NOT relative to the unseen hand but to the visual target the participants were supposed to move their hand to. If the results were converted so to be relative to the unseen hand, the localization biases would be over 20 deg in magnitude.

The PEA simulations are plotted relative to the unseen hand which makes sense. If the authors want to persist using the Tsay 2020 dataset despite any issues, they at least need to make sure that the simulations are mimicking the same change. That is, the data from Tsay 2020 needs to be converted to the same variable used in the current paper.

If the main objection for using the Tsay 2021 is that the design would lead to forgetting, we found that active localization (or any intervening active movements like no-cursor reach) does lead to some interference or forgetting (a small reduction in overall magnitude of adaptation) this is not the case for passive localization, see Ruttle et al, 2021 (data on osf). This was also just a suggestion, there may of course also be other, more suitable data sets.

As stated above, changing the reference system is not necessary, nor does it affect our results. Tsay et al 2020 dataset is unique since it shows the gradual change of reported hand location along with error-clamp adaptation. The forgetting (or reduction in proprioceptive bias), even if it exists, would not affect the fitting quality of our model for the Tsay 2020 dataset: if we assume that forgetting is invariant over the adaptation process, the forgetting would only reduce the proprioceptive bias uniformly across trials. This can be accounted for by a smaller weight on . The critical fact is that the model can explain the gradual drift of the proprioceptive judgment of the hand location.

By the way, Ruttle et al.'s 2021 dataset is not for error-clamp adaptation, and thus we will leave it to test our model extension in the future (after incorporating an explicit process in the model).

References

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Kim, H. E., Parvin, D. E., & Ivry, R. B. (2019). The influence of task outcome on implicit motor learning. ELife, 8. https://doi.org/10.7554/eLife.39882

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Kojima, Y., Iwamoto, Y., & Yoshida, K. (2004). Memory of learning facilitates saccadic adaptation in the monkey. The Journal of Neuroscience: The Official Journal of the Society for Neuroscience, 24(34), 7531–7539.

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Morehead, J. R., Taylor, J. A., Parvin, D. E., & Ivry, R. B. (2017). Characteristics of implicit sensorimotor adaptation revealed by task-irrelevant clamped feedback. Journal of Cognitive Neuroscience, 29(6), 1061–1074.

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Tsay, J. S., Avraham, G., Kim, H. E., Parvin, D. E., Wang, Z., & Ivry, R. B. (2021). The effect of visual uncertainty on implicit motor adaptation. Journal of Neurophysiology, 125(1), 12–22.

Tsay, J. S., Kim, H. E., Saxena, A., Parvin, D. E., Verstynen, T., & Ivry, R. B. (2022). Dissociable use-dependent processes for volitional goal-directed reaching. Proceedings. Biological Sciences / The Royal Society, 289(1973), 20220415.

Tsay, J. S., Kim, H., Haith, A. M., & Ivry, R. B. (2022). Understanding implicit sensorimotor adaptation as a process of proprioceptive re-alignment. ELife, 11, e76639.

Tsay, J. S., Parvin, D. E., & Ivry, R. B. (2020). Continuous reports of sensed hand position during sensorimotor adaptation. Journal of Neurophysiology, 124(4), 1122–1130.

Tsay, J. S., Tan, S., Chu, M. A., Ivry, R. B., & Cooper, E. A. (2023). Low Vision Impairs Implicit Sensorimotor Adaptation in Response to Small Errors, But Not Large Errors. Journal of Cognitive Neuroscience, 35(4), 736–748.

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

eLife assessment

This study presents a valuable finding on the influence of visual uncertainty and Bayesian cue combination on implicit motor adaptation in young healthy participants. The evidence supporting the claims of the authors is solid, although a better discussion of the link between the model variables and the outcomes of related behavioral experiments would strengthen the conclusions. The work will be of interest to researchers in sensory cue integration and motor learning.

Public Reviews:

Reviewer #1 (Public Review):

This valuable study demonstrates a novel mechanism by which implicit motor adaptation saturates for large visual errors in a principled normative Bayesian manner. Additionally, the study revealed two notable empirical findings: visual uncertainty increases for larger visual errors in the periphery, and proprioceptive shifts/implicit motor adaptation are non-monotonic, rather than ramp-like. This study is highly relevant for researchers in sensory cue integration and motor learning. However, I find some areas where statistical quantification is incomplete, and the contextualization of previous studies to be puzzling.

Thank you for your feedback and the positive highlights of our study. We appreciate your insights and will address the concerns in our revisions.

Issue #1: Contextualization of past studies.

While I agree that previous studies have focused on how sensory errors drive motor adaptation (e.g., Burge et al., 2008; Wei and Kording, 2009), I don't think the PReMo model was contextualized properly. Indeed, while PReMo should have adopted clearer language - given that proprioception (sensory) and kinaesthesia (perception) have been used interchangeably, something we now make clear in our new study (Tsay, Chandy, et al. 2023) - PReMo's central contribution is that a perceptual error drives implicit adaptation (see Abstract): the mismatch between the felt (perceived) and desired hand position. The current paper overlooks this contribution. I encourage the authors to contextualize PReMo's contribution more clearly throughout. Not mentioned in the current study, for example, PReMo accounts for the continuous changes in perceived hand position in Figure 4 (Figure 7 in the PReMo study).

There is no doubt that the current study provides important additional constraints on what determines perceived hand position: Firstly, it offers a normative Bayesian perspective in determining perceived hand position. PReMo suggests that perceived hand position is determined by integrating motor predictions with proprioception, then adding a proprioceptive shift; PEA formulates this as the optimal integration of these three inputs. Secondly, PReMo assumed visual uncertainty to remain constant for different visual errors; PEA suggests that visual uncertainty ought to increase (but see Issue #2).

Thank you for the comments and suggestions. We have now incorporated the citation for (Tsay et al., 2024), to acknowledge their clarification on the terms of perceptual error. We also agree that our model differs in two fundamental ways. One is to ditch the concept of proprioceptive shift and its contribution to the perceived hand location; instead, we resort to a “one-shot” integration of three types of cues with Bayesian rules. This is a more elegant and probably more ecological way of processing hand location per Occam's Razor. The second essential change is to incorporate the dependency of visual uncertainty on perturbation size into the model, as opposed to resorting to a ramp function of proprioceptive changes relative to perturbation size. The ramp function is not well grounded in perception studies. Yes, we acknowledged that PReMo is the first to recognize the importance of perceptual error, but highlighted the model differences in our Discussion.

We also think the PReMo model has the potential to explain Fig 4A. But the Tsay et al., 2022 paper assumes that “a generic shift in visual space” explains the gradual proprioceptive changes from negative to positive (see page 17 in Tsay et al., 2022). We do not think that evoking this visual mechanism is necessary to explain Fig 4A; instead, the proprioceptive change is a natural result of hand deviations during implicit adaptation. As the hand moves away from the target (in the positive direction) during adaptation, the estimated hand location goes alone with it. We believe this is the correct way of explaining Fig4A results. As we played around with the PReMo model, we found it is hard to use visual shift to explain this part of data without additional assumptions (at least not with the ones published in Tsay et al., 2022). Furthermore, our PEA model also parsimoniously explains away the proprioceptive shift observed in a completely different setting, i,e., the proprioceptive changes measured by the passive method as a function of perturbation size in Exp 3.

We expanded the discussion about the comparison between the two models, especially about their different views for explaining Fig4A.

Issue #2: Failed replication of previous results on the effect of visual uncertainty.

(2a) A key finding of this paper is that visual uncertainty linearly increases in the periphery; a constraint crucial for explaining the non-monotonicity in implicit adaptation. One notable methodological deviation from previous studies is the requirement to fixate on the target: Notably, in the current experiments, participants were asked to fixate on the target, a constraint not imposed in previous studies. In a free-viewing environment, visual uncertainty may not attenuate as fast, and hence, implicit adaptation does not attenuate as quickly as that revealed in the current design with larger visual errors. Seems like this current fixation design, while important, needs to be properly contextualized considering how it may not represent most implicit adaptation experiments.

First, we don’t think there is any previous study that examined visual uncertainty as a function of perturbation size. Thus, we do not have a replication problem here. Secondly, our data indicate that even without asking people to fixate on the target, people still predominantly fixate on the target during error-clamp adaptation (when they are “free” viewing). For our Exp 1, the fixation on the straight line between the starting position and the target is 86%-95% (as shown in Figure S1 now， also see below). We also collected eye-tracking data in Exp 4, which is a typical error-clamp experiment. More than 95% fall with +/- 50 pixels around the center of the screen, even slightly higher than Exp 1. This is well understandable: the typical error-clamp adaptation requires people to ignore the cursor and move the hand towards the target. To minimize the interference of the concurrently moving cursor, people depend on the fixation on the target, the sole task-relevant visual marker in the workspace, to achieve the task goal.

In sum, forcing the participants to fixate on the target is not because we aimed to make up the linear dependency of visual uncertainty; we required them to do so to mimic the eye-tracking pattern in typical error-clamp learning, which has been revealed in our pilot experiment. The visual uncertainty effect is sound, our study is the first to clearly demonstrate it.

Author response image 1.

On a side note (but an important one), the high percentage of fixation on the aiming target is also true for conventional visuomotor rotation, which involves strategic re-aiming (shown in Bromberg et al., 2019; de Brouwer et al., 2018, we have an upcoming paper to show this). This is one reason that our new theory would also be applicable to other types of motor adaptation.

(2b) Moreover, the current results - visual uncertainty attenuates implicit adaptation in response to large, but not small, visual errors - deviates from several past studies that have shown that visual uncertainty attenuates implicit adaptation to small, but not large, visual errors (Tsay, Avraham, et al. 2021; Makino, Hayashi, and Nozaki, n.d.; Shyr and Joshi 2023). What do the authors attribute this empirical difference to? Would this free-viewing environment also result in the opposite pattern in the effect of visual uncertainty on implicit adaptation for small and large visual errors?

We don’t think all the mentioned previous studies manipulated the visual uncertainty in a parametric way, and none of them provided quantitative measures of visual uncertainty. As we detailed in our Exp4 and in our Discussion, we don’t think Tsay et al., 2021 paper’s manipulation of visual uncertainty is appropriate (see below for 2d). Makino et al., 2023 study used multiple clamped cursors to perturb people, and its effect is not easily accountable since additional processes might be invoked given this kind of complex visual feedback. More importantly, we do not think this is a direct way of modulating visual uncertainty, nor did they provide any evidence.

(2c) In the current study, the measure of visual uncertainty might be inflated by brief presentation times of comparison and referent visual stimuli (only 150 ms; our previous study allowed for a 500 ms viewing time to make sure participants see the comparison stimuli). Relatedly, there are some individuals whose visual uncertainty is greater than 20 degrees standard deviation. This seems very large, and less likely in a free-viewing environment.

For our 2AFC, the reference stimulus is the actual clamped cursor, which lasts for 800 ms. The comparison stimulus is a 150-ms dot representation appearing near the reference. For measuring perception of visual motion, this duration is sufficient as previous studies used similar durations (Egly & Homa, 1984; Owsley et al., 1995). We think the 20-degree standard deviation is reasonable given that people fixate on the target, with only peripheral vision to process the fast moving cursor. The steep linear increase in visual uncertainty about visual motion is well documented. The last author of this paper has shown that the uncertainty of visual motion speed (though not about angels) follows the same steep trend (Wei et al., 2010). It is noteworthy that without using our measured visual uncertainty in Exp1, if we fit the adaptation data in Exp2 to “estimate” the visual uncertainty, they are in fact well aligned with each other (see Figure S7 and Supplementary Text 2). This is a strong support that our estimation is valid and accurate. We think this high visual uncertainty is an important message to the field. Thus we now highlighted its magnitude in our Discussion.

(2d) One important confound between clear and uncertain (blurred) visual conditions is the number of cursors on the screen. The number of cursors may have an attenuating effect on implicit adaptation simply due to task-irrelevant attentional demands (Parvin et al. 2022), rather than that of visual uncertainty. Could the authors provide a figure showing these blurred stimuli (gaussian clouds) in the context of the experimental paradigm? Note that we addressed this confound in the past by comparing participants with and without low vision, where only one visual cursor is provided for both groups (Tsay, Tan, et al. 2023).

Thank you for raising this important point about types of visual stimuli for manipulating uncertainty. We used Gaussian blur of a single cursor (similar to Burge et al., 2008) instead of a cloud of dots. We now added a figure inset to show how this blur looks.

Using a cursor cloud Makino et al., 2023; Tsay et al., 2021 to modulate visual uncertainty has inherent drawbacks that make it unsuitable for visuomotor adaptation. For the error clamp paradigm, the error is defined as angular deviation. The cursor cloud consists of multiple cursors spanning over a range of angles, which affects both the sensory uncertainty (the intended outcome) and the sensory estimate of angles (the error estimate, the undesired outcome). In Bayesian terms, the cursor cloud aims to modulate the sigma of a distribution (sigma_v       in         our       model), but it additionally affects the mean of the distribution (mu). This unnecessary confound is avoided by using cursor blurring, which is still a cursor with its center (mu) unchanged from a single cursor. Furthermore, as correctly pointed out in the original paper by Tsay et al., 2021, the cursor cloud often overlaps with the visual target, this “target hit” would affect adaptation, possibly via a reward learning mechanism (See Kim et al., 2019). This is a second confound that accompanies the cursor cloud.

Issue #3: More methodological details are needed.

(3a) It's unclear why, in Figure 4, PEA predicts an overshoot in terms of perceived hand position from the target. In PReMo, we specified a visual shift in the perceived target position, shifted towards the adapted hand position, which may result in overshooting of the perceived hand position with this target position. This visual shift phenomenon has been discovered in previous studies (e.g., (Simani, McGuire, and Sabes 2007)).

Visual shift, as it is called in Simani et al., 2007, is irrelevant for our task here. The data we are modeling are motor adaptation (hand position changes) and so-called proprioceptive changes (hand localization changes), both are measured and referenced in the extrinsic coordinate, not referenced to a visual target. For instance, the proprioceptive changes are either relative to the actual hand location (Exp 3) or relative to the goal (Fig 4A). We also don’t think visual shift is necessary in explaining the perceptual judgment of an unseen hand (the target shown during the judgment indeed has an effect of reducing the biasing effect of PE, see below for responses to reviewer 3).

In the PEA model, the reported hand angle is the result of integrating cues from the actual hand position and the estimated hand position (x_hand_hat) from previous movements. This integration process leads to the combined reported hand position potentially overshooting or undershooting, depending on the degree of adaptation. It is the changed proprioceptive cue (because the actively moved hand slowly adapted to the error clamp) leading to the overshoot of the perceived hand position.

In Results, we now explain these value changes with parentheses. Model details about the mechanisms of cue combination and model predictions can be found in Supplementary Text 1. We believe these detailed explanations can make this apparent.

(3b) The extent of implicit adaptation in Experiment 2, especially with smaller errors, is unclear. The implicit adaptation function seems to be still increasing, at least by visual inspection. Can the authors comment on this trend, and relatedly, show individual data points that help the reader appreciate the variability inherent to these data?

Indeed, the adaptation for small errors appears not completely saturated with our designated number of trials. However, this will not affect our model analysis. Our model fitting for PEA and other competing models is done on the time-series of adaptation, not on the saturated adaptation extent (see Fig 3A). Thus, despite that some conditions might not produce the full range of adaptation, the data is sufficient to constrain the models. We now mention this concern in Results; we also emphasize that the model not only explains the adaptation magnitude (operationally defined as adaptation extent measured at the same time, i.e., the end of the adaptation phase) but also the full learning process.

In response, we have included individual data points in the revised Figure 3B-D to provide a clear illustration of the extent of implicit adaptation, particularly for small perturbations.

(3c) The same participants were asked to return for multiple days/experiments. Given that the authors acknowledge potential session effects, with attenuation upon re-exposure to the same rotation (Avraham et al. 2021), how does re-exposure affect the current results? Could the authors provide clarity, perhaps a table, to show shared participants between experiments and provide evidence showing how session order may not be impacting results?

Thank you for raising the issue of session and re-exposure effects. First, we don’t think Exp1 has an effect on Exp4. Exp1 is a perceptual task and Exp4 is a motor adaptation task. Furthermore, Exp1 used random visual stimuli on both sides, thus it did not lead to any adaptation effect on its own. Second, Exp4 indeed had three sessions performed on three days, but the session effect does not change our main conclusion about the visual uncertainty. We used a 3-way repeated-measures anova (3 day x 3 perturbation x 2 visual uncertainty) revealed a significant main effect of day (F(2,36) = 17.693, p<0.001), indicating changes in performance across sessions (see Figure below). Importantly, the effects of perturbation and visual uncertainty (including their interactions) remain the same. The day factor did not interact with them. The main effect of day shows that the overall adaptation effect is reduced across days. Post-hoc pairwise comparisons elucidated that single-trial learning (STL) performance on Day 1 was significantly higher than on Day 2 (p = 0.004) and Day 3 (p < 0.001), with no significant difference between Day 2 and Day 3 (p = 0.106). Other ANOVA details: significant main effects for perturbation (F(1,36) = 8.872, p<0.001) and visual uncertainty (F(1,18) = 49.164, p<0.001), as well as a significant interaction between perturbation size and visual uncertainty (F(2,36) = 5.160, p = 0.013). There were no significant interactions involving the day factor with any other factors (all p > 0.182). Thus, the overall adaptation decreases over the days, but the day does not affect our concerned interaction effect of visual uncertainty and perturbation. The fact that their interaction preserved over different sessions strengthened our conclusion about how visual uncertainty systematically affects implicit adaptation.

Author response image 2.

(3d) The number of trials per experiment should be detailed more clearly in the Methods section (e.g., Exp 4). Moreover, could the authors please provide relevant code on how they implemented their computational models? This would aid in future implementation of these models in future work. I, for one, am enthusiastic to build on PEA.

We have clarified the number of trials conducted in each experiment, with detailed information now readily available in the Methods section of the main text. In addition, we have made the code for data analysis and modeling publicly accessible. These resources can be found in the updated "Data Availability" section of our paper.

(3f) In addition to predicting a correlation between proprioceptive shift and implicit adaptation on a group level, both PReMo and PEA (but not causal inference) predict a correlation between individual differences in proprioceptive shift and proprioceptive uncertainty with the extent of implicit adaptation (Tsay, Kim, et al. 2021). Interestingly, shift and uncertainty are independent (see Figures 4F and 6C in Tsay et al, 2021). Does PEA also predict independence between shift and uncertainty? It seems like PEA does predict a correlation.

Thank you for addressing this insightful question. Our PEA model indeed predicts a positive correlation (although not linear) between the proprioceptive uncertainty and the amplitude of the estimated hand position (x_hand_hat). This prediction is consistent with the simulations conducted, using the same parameters that were applied to generate the results depicted in

Figure 4B of our manuscript (there is a sign flip as x_hand_hat is negative).

Author response image 3.

Regarding the absence of a correlation observed in Tsay et al., 2021, we offer several potential explanations for this discrepancy. First, the variability observed in passive hand localization during motor adaptation (as in Tsay et al., 2021) does not directly equal proprioceptive uncertainty, which typically requires psychophysical testing to accurately assess. Second, our study showed that the proprioceptive bias attenuates during the repetitive measurements; in our Exp3, it decreased within a block of three trials. We noticed that Tsay et al., 2021 study used 36 measurements in a row without interleaving adaptation trials. Thus, the “averaged” proprioceptive bias in Tsay’s study might not reflect the actual bias during adaptation. We also noticed that that study showed large individual differences in both proprioceptive bias and proprioceptive variability (not uncertainty), thus getting a positive result, if it were really there, would require a large number of participants, probably larger than their n=30ish sample size. These putative explanations are not put in the revision, which already has a long discussion and has no space for discussing about a null result.

Reviewer #2 (Public Review):

Summary:

The authors present the Perceptual Error Adaptation (PEA) model, a computational approach offering a unified explanation for behavioral results that are inconsistent with standard state-space models. Beginning with the conventional state-space framework, the paper introduces two innovative concepts. Firstly, errors are calculated based on the perceived hand position, determined through Bayesian integration of visual, proprioceptive, and predictive cues. Secondly, the model accounts for the eccentricity of vision, proposing that the uncertainty of cursor position increases with distance from the fixation point. This elegantly simple model, with minimal free parameters, effectively explains the observed plateau in motor adaptation under the implicit motor adaptation paradigm using the error-clamp method. Furthermore, the authors experimentally manipulate visual cursor uncertainty, a method established in visuomotor studies, to provide causal evidence. Their results show that the adaptation rate correlates with perturbation sizes and visual noise, uniquely explained by the PEA model and not by previous models. Therefore, the study convincingly demonstrates that implicit motor adaptation is a process of Bayesian cue integration

Strengths:

In the past decade, numerous perplexing results in visuomotor rotation tasks have questioned their underlying mechanisms. Prior models have individually addressed aspects like aiming strategies, motor adaptation plateaus, and sensory recalibration effects. However, a unified model encapsulating these phenomena with a simple computational principle was lacking. This paper addresses this gap with a robust Bayesian integration-based model. Its strength lies in two fundamental assumptions: motor adaptation's influenced by visual eccentricity, a well-established vision science concept, and sensory estimation through Bayesian integration. By merging these well-founded principles, the authors elucidate previously incongruent and diverse results with an error-based update model. The incorporation of cursor feedback noise manipulation provides causal evidence for their model. The use of eye-tracking in their experimental design, and the analysis of adaptation studies based on estimated eccentricity, are particularly elegant. This paper makes a significant contribution to visuomotor learning research.

Weaknesses:

The paper provides a comprehensive account of visuomotor rotation paradigms, addressing incongruent behavioral results with a solid Bayesian integration model. However, its focus is narrowly confined to visuomotor rotation, leaving its applicability to broader motor learning paradigms, such as force field adaptation, saccadic adaptation, and de novo learning paradigms, uncertain. The paper's impact on the broader fields of neuroscience and cognitive science may be limited due to this specificity. While the paper excellently demonstrates that specific behavioral results in visuomotor rotation can be explained by Bayesian integration, a general computational principle, its contributions to other motor learning paradigms remain to be explored. The paper would benefit from a discussion on the model's generality and its limitations, particularly in relation to the undercompensating effects in other motor learning paradigms.

Thank you for your thoughtful review and recognition of the contributions our work makes towards understanding implicit motor adaptation through the Perceptual Error Adaptation (PEA) model. We appreciate your suggestion to broaden the discussion about the model's applicability beyond the visuomotor rotation paradigm, a point we acknowledge was not sufficiently explored in our initial discussion.

Our model is not limited to the error-clamp adaptation, where the participants were explicitly told to ignore the rotated cursor. The error-clamp paradigm is one rare example that implicit motor learning can be isolated in a nearly idealistic way. Our findings thus imply two key aspects of implicit adaptation: 1) localizing one’s effector is implicitly processed and continuously used to update the motor plan; 2) Bayesian cue combination is at the core of integrating movement feedback and motor-related cues (motor prediction cue in our model) when forming procedural knowledge for action control.

We will propose that the same two principles should be applied to various kinds of motor adaptation and motor skill learning, which constitutes motor learning in general. Most of our knowledge about motor adaptation is from visuomotor rotation, prism adaptation, force field adaptation, and saccadic adaptation. The first three types all involve localizing one’s effector under the influence of perturbed sensory feedback, and they also have implicit learning. We believe they can be modeled by variants of our model, or at least should consider using the two principles we laid out above to think of their computational nature. For skill learning, especially for de novo learning, the area still lacks a fundamental computational model that accounts for skill acquisition process on the level of relevant movement cues. Our model suggests a promising route, i.e., repetitive movements with a Bayesian cue combination of movement-related cues might underlie the implicit process of motor skills.

We added more discussion on the possible broad implications of our model in the revision.

Reviewer #3 (Public Review):

Summary

In this paper, the authors model motor adaptation as a Bayesian process that combines visual uncertainty about the error feedback, uncertainty about proprioceptive sense of hand position, and uncertainty of predicted (=planned) hand movement with a learning and retention rate as used in state space models. The model is built with results from several experiments presented in the paper and is compared with the PReMo model (Tsay, Kim, et al., 2022) as well as a cue combination model (Wei & Körding, 2009). The model and experiments demonstrate the role of visual uncertainty about error feedback in implicit adaptation.

In the introduction, the authors notice that implicit adaptation (as measured in error-clamp-based paradigms) does not saturate at larger perturbations, but decreases again (e.g. Moorehead et al., 2017 shows no adaptation at 135{degree sign} and 175{degree sign} perturbations). They hypothesized that visual uncertainty about cursor position increases with larger perturbations since the cursor is further from the fixated target. This could decrease the importance assigned to visual feedback which could explain lower asymptotes.

The authors characterize visual uncertainty for 3 rotation sizes in the first experiment, and while this experiment could be improved, it is probably sufficient for the current purposes. Then the authors present a second experiment where adaptation to 7 clamped errors is tested in different groups of participants. The models' visual uncertainty is set using a linear fit to the results from experiment 1, and the remaining 4 parameters are then fit to this second data set. The 4 parameters are 1) proprioceptive uncertainty, 2) uncertainty about the predicted hand position, 3) a learning rate, and 4) a retention rate. The authors' Perceptual Error Adaptation model ("PEA") predicts asymptotic levels of implicit adaptation much better than both the PReMo model (Tsay, Kim et al., 2022), which predicts saturated asymptotes, or a causal inference model (Wei & Körding, 2007) which predicts no adaptation for larger rotations. In a third experiment, the authors test their model's predictions about proprioceptive recalibration, but unfortunately, compare their data with an unsuitable other data set. Finally, the authors conduct a fourth experiment where they put their model to the test. They measure implicit adaptation with increased visual uncertainty, by adding blur to the cursor, and the results are again better in line with their model (predicting overall lower adaptation) than with the PReMo model (predicting equal saturation but at larger perturbations) or a causal inference model (predicting equal peak adaptation, but shifted to larger rotations). In particular, the model fits experiment 2 and the results from experiment 4 show that the core idea of the model has merit: increased visual uncertainty about errors dampens implicit adaptation.

Strengths

In this study, the authors propose a Perceptual Error Adaptation model ("PEA") and the work combines various ideas from the field of cue combination, Bayesian methods, and new data sets, collected in four experiments using various techniques that test very different components of the model. The central component of visual uncertainty is assessed in the first experiment. The model uses 4 other parameters to explain implicit adaptation. These parameters are 1) learning and 2) retention rate, as used in popular state space models, and the uncertainty (variance) of 3) predicted and 4) proprioceptive hand position. In particular, the authors observe that asymptotes for implicit learning do not saturate, as claimed before, but decrease again when rotations are very large and that this may have to do with visual uncertainty (e.g. Tsay et al., 2021, J Neurophysiol 125, 12-22). The final experiment confirms predictions of the fitted model about what happens when visual uncertainty is increased (overall decrease of adaptation). By incorporating visual uncertainty depending on retinal eccentricity, the predictions of the PEA model for very large perturbations are notably different from and better than, the predictions of the two other models it is compared to. That is, the paper provides strong support for the idea that visual uncertainty of errors matters for implicit adaptation.

Weaknesses

Although the authors don't say this, the "concave" function that shows that adaptation does not saturate for larger rotations has been shown before, including in papers cited in this manuscript.

The first experiment, measuring visual uncertainty for several rotation sizes in error-clamped paradigms has several shortcomings, but these might not be so large as to invalidate the model or the findings in the rest of the manuscript. There are two main issues we highlight here. First, the data is not presented in units that allow comparison with vision science literature. Second, the 1 second delay between the movement endpoint and the disappearance of the cursor, and the presentation of the reference marker, may have led to substantial degradation of the visual memory of the cursor endpoint. That is, the experiment could be overestimating the visual uncertainty during implicit adaptation.

The paper's third experiment relies to a large degree on reproducing patterns found in one particular paper, where the reported hand positions - as a measure of proprioceptive sense of hand position - are given and plotted relative to an ever-present visual target, rather than relative to the actual hand position. That is, 1) since participants actively move to a visual target, the reported hand positions do not reflect proprioception, but mostly the remembered position of the target participants were trying to move to, and 2) if the reports are converted to a difference between the real and reported hand position (rather than the difference between the target and the report), those would be on the order of ~20{degree sign} which is roughly two times larger than any previously reported proprioceptive recalibration, and an order of magnitude larger than what the authors themselves find (1-2{degree sign}) and what their model predicts. Experiment 3 is perhaps not crucial to the paper, but it nicely provides support for the idea that proprioceptive recalibration can occur with error-clamped feedback.

Perhaps the largest caveat to the study is that it assumes that people do not look at the only error feedback available to them (and can explicitly suppress learning from it). This was probably true in the experiments used in the manuscript, but unlikely to be the case in most of the cited literature. Ignoring errors and suppressing adaptation would also be a disastrous strategy to use in the real world, such that our brains may not be very good at this. So the question remains to what degree - if any - the ideas behind the model generalize to experiments without fixation control, and more importantly, to real-life situations.

Specific comments:

A small part of the manuscript relies on replicating or modeling the proprioceptive recalibration in a study we think does NOT measure proprioceptive recalibration (Tsay, Parvin & Ivry, JNP, 2020). In this study, participants reached for a visual target with a clamped cursor, and at the end of the reach were asked to indicate where they thought their hand was. The responses fell very close to the visual target both before and after the perturbation was introduced. This means that the difference between the actual hand position, and the reported/felt hand position gets very large as soon as the perturbation is introduced. That is, proprioceptive recalibration would necessarily have roughly the same magnitude as the adaptation displayed by participants. That would be several times larger than those found in studies where proprioceptive recalibration is measured without a visual anchor. The data is plotted in a way that makes it seem like the proprioceptive recalibration is very small, as they plot the responses relative to the visual target, and not the discrepancy between the actual and reported hand position. It seems to us that this study mostly measures short-term visual memory (of the target location). What is astounding about this study is that the responses change over time to begin with, even if only by a tiny amount. Perhaps this indicates some malleability of the visual system, but it is hard to say for sure.

Regardless, the results of that study do not form a solid basis for the current work and they should be removed. We would recommend making use of the dataset from the same authors, who improved their methods for measuring proprioception shifts just a year later (Tsay, Kim, Parvin, Stover, and Ivry, JNP, 2021). Although here the proprioceptive shifts during error-clamp adaptation (Exp 2) were tiny, and not quite significant (p<0.08), the reports are relative to the actual location of the passively placed unseen hand, measured in trials separate from those with reach adaptation and therefore there is no visual target to anchor their estimates to.

Experiment 1 measures visual uncertainty with increased rotation size. The authors cite relevant work on this topic (Levi & Klein etc) which has found a linear increase in uncertainty of the position of more and more eccentrically displayed stimuli.

First, this is a question where the reported stimuli and effects could greatly benefit from comparisons with the literature in vision science, and the results might even inform it. In order for that to happen, the units for the reported stimuli and effects should (also) be degrees of visual angle (dva).

As far as we know, all previous work has investigated static stimuli, where with moving stimuli, position information from several parts of the visual field are likely integrated over time in a final estimate of position at the end of the trajectory (a Kalman filter type process perhaps). As far as we know, there are no studies in vision science on the uncertainty of the endpoint of moving stimuli. So we think that the experiment is necessary for this study, but there are some areas where it could be improved.

Then, the linear fit is done in the space of the rotation size, but not in the space of eccentricity relative to fixation, and these do not necessarily map onto each other linearly. If we assume that the eye-tracker and the screen were at the closest distance the manufacturer reports it to work accurately at (45 cm), we would get the largest distances the endpoints are away from fixation in dva. Based on that assumed distance between the participant and monitor, we converted the rotation angles to distances between fixation and the cursor endpoint in degrees visual angle: 0.88, 3.5, and 13.25 dva (ignoring screen curvature, or the absence of it). The ratio between the perturbation angle and retinal distance to the endpoint is roughly 0.221, 0.221, and 0.207 if the minimum distance is indeed used - which is probably fine in this case. But still, it would be better to do fit in the relevant perceptual coordinate system.

The first distance (4 deg rotation; 0.88 dva offset between fixation and stimulus) is so close to fixation (even at the assumed shortest distance between eye and screen) that it can be considered foveal and falls within the range of noise of eye-trackers + that of the eye for fixating. There should be no uncertainty on or that close to the fovea. The variability in the data is likely just measurement noise. This also means that a linear fit will almost always go through this point, somewhat skewing the results toward linearity. The advantage is that the estimate of the intercept (measurement noise) is going to be very good. Unfortunately, there are only 2 other points measured, which (if used without the closest point) will always support a linear fit. Therefore, the experiment does not seem suitable to test linearity, only to characterize it, which might be sufficient for the current purposes. We'd understand if the effort to do a test of linearity using many more rotations requires too much effort. But then it should be made much clearer that the experiment assumes linearity and only serves to characterize the assumed linearity.

Final comment after the consultation session:

There were a lot of discussions about the actual interpretation of the behavioral data from this paper with regards to past papers (Tsay et al. 2020 or 2021), and how it matches the different variables of the model. The data from Tsay 2020 combined both proprioceptive information (Xp) and prediction about hand position (Xu) because it involves active movements. On the other hand, Tsay et al. 2021 is based on passive movements and could provide a better measure of Xp alone. We would encourage you to clarify how each of the variables used in the model is mapped onto the outcomes of the cited behavioral experiments.

The reviewers discussed this point extensively during the consultation process. The results reported in the Tsay 2020 study reflect both proprioception and prediction. However, having a visual target contributes more than just prediction, it is likely an anchor in the workspace that draws the response to it. Such that the report is dominated by short-term visual memory of the target (which is not part of the model). However, in the current Exp 3, as in most other work investigating proprioception, this is calculated relative to the actual direction.

The solution is fairly simple. In Experiment 3 in the current study, Xp is measured relative to the hand without any visual anchors drawing responses, and this is also consistent with the reference used in the Tsay et al 2021 study and from many studies in the lab of D. Henriques (none of which also have any visual reach target when measuring proprioceptive estimates). So we suggest using a different data set that also measures Xp without any other influences, such as the data from Tsay et al 2021 instead.

These issues with the data are not superficial and can not be solved within the model. Data with correctly measured biases (relative to the hand) that are not dominated by irrelevant visual attractors would actually be informative about the validity of the PEA model. Dr. Tsay has so much other that we recommend using a more to-the-point data set that could actually validate the PEA model.

As the comments are repetitive at some places, we summarize them into three questions and address it one by one below:

(1) Methodological Concerns about visual uncertainty estimation in Experiment 1: a) the visual uncertainty is measured in movement angles (degrees), while the unit in vision science is in visual angles (vda). This mismatch of unit hinders direct comparison between the found visual uncertainty and those reported in the literature, and b) a 1-second delay between movement endpoint and the reference marker presentation causes an overestimate of visual uncertainty due to potential degradation of visual memory. c) The linear function of visual uncertainty is a result of having only three perturbation sizes.

a) As noted by the reviewer, our visual uncertainty is about cursor motion direction in the display plane, which has never been measured before. We do not think our data is comparable to any findings in visual science about fovea/peripheral comparison. We quoted Klein and others’ work Klein & Levi, 1987; Levi et al., 1987 in vision science since their studies showed that the deviation from the fixation is associated with the increase in visual uncertainty. Their study thus inspired our Exp1 to probe how our concerned visual uncertainty (specifically for visual motion direction) changes with an increasing deviation from the fixation. We believe that any model and its model parameters should be specifically tailored to the task or context it tries to emulate. In our case, motion direction in a center-out reaching setting is the modeled context, and all the relevant model parameters should be specified in movement angles.

b) The 1s delay of the reference cursor appears to have minimum impact on the estimate of visual uncertainty, based on previous vision studies. Our Exp1 used a similar visual paradigm by White et al., 1992, which shows that delay does not lead to an increase in visual uncertainty over a broad range of values (from 0.2s to >1s, see their Figure 5-6). We will add more methodology justifications in our revision.

c) We agree that if more angles are tested we can be more confident about the linearity of visual uncertainty. However, the linear function is a good approximation of visual uncertainty (as shown in Figure 2C). More importantly, our model performance does not hinge on a strict linear function. Say, if it is a power function with an increasing slope, our model will still predict the major findings presented in the paper, as correctly pointed out by the reviewer. It is the increasing trend of visual uncertainty, which is completely overlooked by previous studies, that lead to various seemingly puzzling findings in implicit adaptation. Lastly, without assuming a linear function, we fitted the large dataset of motor adaptation from Exp2 to numerically estimate the visual uncertainty. This estimated visual uncertainty has a strong linear relationship with perturbation size (R = 0.991, p<0.001). In fact, the model-fitted visual uncertainty is very close to the values we obtained in Exp1. We now included this analysis in the revision. See details in Supplementary text 2 and Figure S7.

(2) Experiment 3's: the reviewer argues that the Tsay et al., 2020 data does not accurately measure proprioceptive recalibration, thus it is not suitable for showing our model’s capacity in explaining proprioceptive changes during adaptation.

Response: We agree that the data from Tsay et al., 2020 is not from passive localization, which is regarded as the widely-accepted method to measure proprioceptive recalibration, a recalibration effect in the sensory domain. The active localization, as used in Tsay et al., 2020, is hypothesized as closely related to people’s forward prediction (where people want to go as the reviewer put it in the comments). However, we want to emphasize that we never equated Tsay’s findings as proprioceptive recalibration: throughout the paper we call them “reported hand location”. We reserved “proprioceptive recalibration” to our own Exp3, which used a passive localization method. Thus, we are not guilty of using this term. Secondly, as far as we know, localization bias or changes, no matter measured by passive or active methods, have not been formally modeled quantitatively. We believe our model can explain both, at least in the error-clamp adaptation setting here. Exp3 is for passive localization, the proprioceptive bias is caused by the biasing effect from the just-perceived hand location (X_hand_hat) from the adaptation trial. Tsay et al. 2020 data is for active localization, whose bias shows a characteristic change from negative to positive. This can be explained by just-perceived hand location (X_hand_hat again) and a gradually-adapting hand (X_p). We think this is a significant advance in the realm of proprioceptive changes in adaptation. Of course, our idea can be further tested in other task conditions, e.g., conventional visuomotor rotation or even gain adaptation, which should be left for future studies.

For technical concerns, Tsay et al., 2020 data set is not ideal: when reporting hand location, the participants view the reporting wheel as well as the original target. As correctly pointed out by the reviewer, the presence of the target might provide an anchoring cue for perceptual judgment, which acts as an attractor for localization. If it were the case, our cue combination would predict that this extra attractor effect would lead to a smaller proprioceptive effect than that is currently reported in their paper. The initial negative bias will be closer to the target (zero), and the later positive bias will be closer to the target too. However, the main trend will remain, i.e. the reported hand location would still show the characteristic negative-to-positive change. The attractor effect of the target can be readily modeled by giving less weight to the just-perceived hand location (X_hand_hat). Thus, we would like to keep Tsay et al., 2020 data in our paper but add some explanations of the limitations of this dataset as well as how the model would fare with these limitations.

That being said, our model can explain away both passive and active localization during implicit adaptation elicited by error clamp. The dataset from Tsay et al., 2021 paper is not a good substitute for their 2020 paper in terms of modeling, since that study interleaved some blocks of passive localization trials with adaptation trials. This kind of block design would lead to forgetting of both adaptation (Xp in our model) and the perceived hand (X_hand_hat in our model), the latter is still not considered in our model yet. As our Exp3, which also used passive localization, shows, the influence of the perceived hand on proprioceptive bias is short-lived, up to three trials without adaptation trials. Of course, it would be of great interest to design future studies to study how the proprioceptive bias changes over time, and how its temporal changes relate to the perceptual error. Our model provides a testbed to move forward in this direction.

(3) The reviewer raises concerns about the study's assumption that participants ignore error feedback, questioning the model's applicability to broader contexts and real-world scenarios where ignoring errors might not be viable or common.

Reviewer 2 raised the same question above. We moved our responses here. “We appreciate your suggestion to broaden the discussion about the model's applicability beyond the visuomotor rotation paradigm, a point we acknowledge was not sufficiently explored in our initial discussion.

Our model is not limited to the error-clamp adaptation, where the participants were explicitly told to ignore the rotated cursor. The error-clamp paradigm is one rare example that implicit motor learning can be isolated in a nearly idealistic way. Our findings thus imply two key aspects of implicit adaptation: 1) localizing one’s effector is implicitly processed and continuously used to update the motor plan; 2) Bayesian cue combination is at the core of integrating movement feedback and motor-related cues (motor prediction cue in our model) when forming procedural knowledge for action control.

We will propose that the same two principles should be applied to various kinds of motor adaptation and motor skill learning, which constitutes motor learning in general. Most of our knowledge about motor adaptation is from visuomotor rotation, prism adaptation, force field adaptation, and saccadic adaptation. The first three types all involve localizing one’s effector under the influence of perturbed sensory feedback, and they also have implicit learning. We believe they can be modeled by variants of our model, or at least should consider using the two principles we laid out above to think of their computational nature. For skill learning, especially for de novo learning, the area still lacks a fundamental computational model that accounts for skill acquisition process on the level of relevant movement cues. Our model suggests a promising route, i.e., repetitive movements with a Bayesian cue combination of movement-related cues might underlie the implicit process of motor skills.”

We also add one more important implication of our model: as stated above, our model also explains that the proprioceptive changes, revealed by active or passive localization methods, are brought by (mis)perceived hand localization via Bayesian cue combination. This new insight, though only tested here using the error-clamp paradigm, can be further utilized in other domains, e.g., conventional visuomotor rotation or force field adaptation. We hope this serves as an initial endeavor in developing some computational models for proprioception studies. Please see the extended discussion on this matter in the revision.

Recommendations for the authors:

Revisions:

All three reviewers were positive about the work and have provided a set of concrete and well-aligned suggestions, which the authors should address in a revised version of the article. These are listed below.

A few points of particular note:

(1) There are a lot of discussions about the actual interpretation of behavioral data from this paper or past papers (Tsay et al. 2020 or 2021) and how it matches the different variables of the model.

(2) There are some discussions on the results of the first experiment, both in terms of how it is reported (providing degrees of visual angle) and how it is different than previous results (importance of the point of fixation). We suggest also discussing a few papers on eye movements during motor adaptation from the last years (work of Anouk de Brouwer and Opher Donchin). Could the authors also discuss why they found opposite results to that of previous visual uncertainty studies (i.e., visual uncertainty attenuates learning with large, but not small, visual errors); rather than the other way around as in Burge et al and Tsay et al 2021 and Makino Nozaki 2023 (where visual uncertainty attenuates small, but not large, visual errors).

(3) It is recommended by several reviewers to discuss the applicability of the model to other areas/perturbations.

(4) Several reviewers and I believe that the impact of the paper would be much higher if the code to reproduce all the simulations of the model is made available to the readers. In addition, while I am very positive about the fact that the authors shared the data of their experiments, metadata seems to be missing while they are highly important because these data are otherwise useless.

Thank you for the concise summary of the reviewers’ comments. We have addressed their concerns point by point.

Reviewer #2 (Recommendations For The Authors):

L142: The linear increase in visual uncertainty should be substantiated by previous research in vision science. Please cite relevant papers and discuss why the linear model is considered reasonable.

We cited relevant studies in vision science. Their focus is more about eccentricity inflate visual uncertainty, similar to our findings that deviations from the fixation direction inflate visual uncertainty about motion direction.

We also want to add that our model performance does not hinge on a strict linear function of visual uncertainty. Say, if it is a power function with an increasing slope, our model will still predict the major findings presented in the paper. It is the increasing trend of visual uncertainty, which is completely overlooked by previous studies, that lead to various seemingly puzzling findings in implicit adaptation. Furthermore, without assuming a linear function, we fitted the large dataset of motor adaptation from Exp2 to numerically estimate the visual uncertainty. This estimated visual uncertainty has a strong linear relationship with perturbation size (R = 0.991, p<0.001). In fact, the model-fitted visual uncertainty is very close to the values we obtained in Exp1. We now included this new analysis in the revision. See details in Supplementary text 2 and Figure S7.

L300: I found it challenging to understand the basis for this conclusion. Additional explanatory support is required.

We unpacked this concluding sentence as follows:

“The observed proprioceptive bias is formally modeled as a result of the biasing effect of the perceived hand estimate x_hand_hat. In our mini-block of passive localization, the participants neither actively moved nor received any cursor perturbations for three trials in a row. Thus, the fact that the measured proprioceptive bias is reduced to nearly zero at the third trial suggests that the effect of perceived hand estimate x_hand_hat decays rather rapidly.”

L331: For the general reader, a visual representation of what the blurring mask looks like would be beneficial.

Thanks for the nice suggestion. We added pictures of a clear and a blurred cursor in Figure 5D.

L390: This speculation is intriguing. It would be helpful if the authors explained why they consider causal inference to operate at an explicit process level, as the reasoning is not clear here, although the idea seems plausible.

Indeed, our tentative conclusion here is only based on the model comparison results here. It is still possible that causal inference also work for implicit adaptation besides explicit adaptation. We make a more modest conclusion in the revision:

“The casual inference model is also based on Bayesian principle, then why does it fail to account for the implicit adaptation? We postulate that the failure of the causal inference model is due to its neglect of visual uncertainty as a function of perturbation size, as we revealed in Experiment 1. In fact, previous studies that advocating the Bayesian principle in motor adaptation have largely focused on experimentally manipulating sensory cue uncertainty to observe its effects on adaptation (Burge et al., 2008; He et al., 2016; Körding & Wolpert, 2004; Wei & Körding, 2010), similar to our Experiment 4. Our findings suggest that causal inference of perturbation alone, without incorporating visual uncertainty, cannot fully account for the diverse findings in implicit adaptation. The increase in visual uncertainty by perturbation size is substantial: our Experiment 1 yielded an approximate seven-fold increase from a 4° perturbation to a 64° perturbation. We have attributed this to the fact that people fixate in the desired movement direction during movements. Interestingly, even for conventional visuomotor rotation paradigm where people are required to “control” the perturbed cursor, their fixation is also on the desired direction, not on the cursor itself (de Brouwer, Albaghdadi, et al., 2018; de Brouwer, Gallivan, et al., 2018). Thus, we postulate that a similar hike in visual uncertainty in other “free-viewing” perturbation paradigms. Future studies are warranted to extend our PEA model to account for implicit adaptation in other perturbation paradigms.”

L789: The method of estimating Sigma_hand in the brain was unclear. Since Bayesian computation relies on the magnitude of noise, the cognitive system must have estimates of this noise. While vision and proprioception noise might be directly inferred from signals, the noise of the hand could be deduced from the integration of these observations or an internal model estimate. This process of estimating noise magnitude is theorized in recursive Bayesian integration models (or Kalman filtering), where the size estimate of the state noise (sigma_hand) is updated concurrently with the state estimate (x_hand hat). The equation in L789 and the subsequent explanation appear to assume a static model of noise estimation. However, in practice, the noise parameters, including Sigma_hand, are likely dynamic and updated with each new observation. A more detailed explanation of how Sigma_hand is estimated and its role in the cognitive process.

This is a great comment. In fact, if a Kalman filter is used, the learning rate and the state noise all should be dynamically updated on each trial, under the influence of the observed (x_v). In fact, most adaptation models assume a constant learning rate, including our model here. But a dynamic learning rate (B in our model) is something worth trying. However, in our error-clamp setting, x_v is a constant, thus this observation variable cannot dynamically update the Kalman filter; that’s why we opt to use a “static” Bayesian model to explain our datasets. Thus, Sigma_hand can be estimated by using Bayesian principles as a function of three cues available, i.e., the proprioceptive cue, the visual cue, and the motor prediction cue. We added a

detailed derivation of sigma_hand in the revision in Supplementary text 1.

Reviewer #3 (Recommendations For The Authors):

We observed values in Fig 2C for the 64-degree perturbation that seem to be outliers, i.e., greater than 50 degrees. It is unclear how a psychometric curve could have a "slope" or JNP of over 60, especially considering that the tested range was only 60. Since the data plotted in panel C is a collapse of the signed data in panel B, it is perplexing how such large data points were derived, particularly when the signed uncertainty values do not appear to exceed 30.

Related to the previous point, we would also recommend connecting individual data points: if the uncertainty increases (linearly or otherwise), then people with low uncertainty at the middle distance should also have low uncertainty at the high distance, and people with high uncertainty at one point, should also have that at other distances. Or perhaps the best way to go about this is to use the uncertainty at the two smaller perturbations to predict uncertainty at the largest perturbation for each participant individually?

Thank you for your suggestion to examine the consistency of individual levels of visual uncertainty across perturbation sizes. First, a sigma_v of 60 degrees is well possible, naturally falling out of the experimental data. It shows some individuals indeed have large visual uncertainty. Given these potential outliers (which should not be readily removed as we don’t have any reason to do so), we estimated the linear function of sigma_v with a robust method, i.e., the GLM with a gamma distribution, which favors right-skewed distribution that can well capture positive outliers. Furthermore, we added in our revision a verification test of our estimates of sigma_v: we used Exp2’s adaptation data to estimate sigma_v without assuming its linear dependency. As shown, the model-fitted sigma_v closely matched the estimated ones from Exp1 (see Supplementary text 2 and Figure S7).

We re-plotted the sigma_v with connected data points provided, and the data clearly indicate that individuals exhibit consistent levels of visual uncertainty across different perturbation sizes, i.e. those with relatively lower uncertainty at middle distances (in fact, angles) tend to exhibit relatively lower uncertainty at higher distances too, and similarly, those with higher uncertainty at one distance maintain that level of uncertainty at other distances. This is confirmed by spearman correlation analysis to assess the consistency of uncertainties across different degrees of perturbation among individuals. Again, we observed significant correlations between perturbation angles, indicating good individual consistency (4 and 16 degrees, rho = 0.759, p<0.001; 16 and 64 degrees, rho = 0.527, p = 0.026).

Author response image 4.

The illustration in Fig 2A does not seem to show a stimulus that is actually used in the experiment (looks like about -30{degree sign} perturbation). It would be good to show all possible endpoints with all other visual elements to scale - including the start-points of the PEST procedure.

Thanks for the suggestion. We updated Fig 2A to show a stimulus of +16 degree, as well as added an additional panel to show all the possible endpoints.

Finally (related to the previous point), in lines 589-591 it says the target is a blue cross. Then in lines 614-616, it says participants are to fixate the blue cross or the start position. The start position was supposed to have disappeared, so perhaps the blue plus moved to the start position (which could be the case, when looking at the bottom panel in Fig 2A, although in the illustration the plus did not move fully to the start position, just toward it to some degree). Perhaps the descriptions need to be clarified, or it should be explained why people had to make an eye movement before giving their judgments. And if people could have made either 1) no eye movement, but stayed at fixation, 2) moved to the blue plus as shown in the last panel in Fig 2A, or 3) fixated on the home position, we'd be curious to know if this affected participants' judgments.

Thanks for pointing that out. The blue cross serves as the target in the movement task, then disappears with the cursor after 800ms of frozen time. The blue cross then appeared in the discrimination task at the center of the screen, i.e. the start location. Subjects were asked to fixate at the blue cross during the visual discrimination task. Note this return the fixation to the home position is exactly what we will see in typical error-clamp adaptation: once the movement is over, people guided their hand back to the home position. We performed a pilot study to record the typical fixation pattern during error-clamp adaptation, and Exp1 was intentionally designed to mimic its fixation sequence. We have now updated the description of Figure 2A, emphasizing the stimulus sequence. .

In Figure 4A, the label "bias" is confusing as that is used for recalibrated proprioceptive sense of hand position as well as other kinds of biases elsewhere in the paper. What seems to be meant is the integrated hand position (x-hat_hand?) where all three signals are apparently combined. The label should be changed and/or it should be clarified in the caption.

Thanks for pointing that out, it should be x_hand_hat, and we have corrected this in the revised version of Figure 4.

In the introduction, it is claimed that larger perturbations have not been tested with "implicit adaptation" paradigms, but in the same sentence, a paper is cited (Moorehead et al., 2017) that tests a rotation on the same order of magnitude as the largest one tested here (95{degree sign}), as well as much larger rotations (135{degree sign} and 175{degree sign}). With error-clamps. Interestingly, there is no adaptation in those conditions, which seems more in line with the sensory cue integration model. Can the PEA model explain these results as well? If so, this should be included in the paper, and if not, it should be discussed as a limitation.

First, we double checked our manuscript and found that we never claimed that larger perturbations had not been tested.

We agree that it is always good to have as many conditions as possible. However, the 135 and 175 degree conditions would lead to minimum adaptation, which would not help much in terms of model testing. We postulated that this lack of adaptation is simply due to the fact that people cannot see the moving cursor, or some other unknown reasons. Our simple model is not designed to cover those kinds of extreme cases.

Specify the size of the arc used for the proprioceptive tests in Exp 3 and describe the starting location of the indicator (controlled by the left hand). Ideally, the starting location should have varied across trials to avoid systematic bias.

Thank you for the comments. The size of the arc used during these tests, as detailed in the methods section of our paper, features a ring with a 10 cm radius centered at the start position. This setup is visually represented as a red arc in Figure 7B.

After completing each proprioceptive test trial, participants were instructed to position the indicator at approximately -180° on the arc and then relax their left arm. Although the starting location for the subsequent trial remained at-180°, it was not identical for every trial, thereby introducing slight variability.

Please confirm that the proprioceptive biases plotted in Fig 4E are relative to the baseline.

Thank you for bringing this to our attention. Yes, the proprioceptive biases illustrated in Figure 4E are indeed calculated relative to the baseline measurements. We have added this in the method part.

Data availability: the data are available online, but there are some ways this can be improved. First, it would be better to use an open data format, instead of the closed, proprietary format currently used. Second, there is no explanation for what's in the data, other than the labels. (What are the units? What preprocessing was done?) Third, no code is made available, which would be useful for a computational model. Although rewriting the analyses in a non-proprietary language (to increase accessibility) is not a reasonable request at this point in the project, I'd encourage it for future projects. But perhaps Python, R, or Julia code that implements the model could be made available as a notebook of sorts so that other labs could look at (build on) the model starting with correct code - increasing the potential impact of this work.

Great suggestions. We are also fully supportive of open data and open science. We now:

(1) Updated our data and code repository to include the experimental data in an open data format (.csv) for broader accessibility.

(2) The data are now accompanied by detailed descriptions to clarify their contents.

(3) We have made the original MATLAB (.m) codes for data analysis, model fitting and simulation available online.

(4) We also provide the codes in Jupyter Notebook (.ipynb) formats.

These updates can be found in the revised “Data Availability” section of our manuscript.

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

…I find the concept and execution of the study very interesting and elegant. The paper is also commendably clear and readable. The differences between primary and higher cortex are compelling and I am largely convinced by the authors' claim that they have found evidence that broadly supports a mixed selectivity model of neural disentanglement along the lines of Rigotti et al (2013). I think that the increasing body of evidence for these kinds of representations is a significant development in our understanding of higher sensory representations. I also think that the dDR method is likely to be useful to researchers in a variety of fields who are looking to perform similar types of neural decoding analysis.

Thanks! We agree that questions around population coding and high-level representations are critical in the field of sensory systems.

Reviewer #2 (Public Review):

... This is a well-carried out study with thoughtful analyses which in large part achieves its aims to evaluate how task-engagement changes neural activity across multiple auditory regions. As with all work, there are several caveats or areas for future study/analysis. First, the sounds used here (tones, and narrow-band noise) are relatively simple sounds; previous work suggests that exactly what activity is observed within each region (e.g., sensory only, decision-related, etc) may depend in part upon what stimuli are used. Therefore, while the current study adds importantly to the literature, future work may consider the use of more varied stimuli. Second, the animals here were engaged in a behavioral task; but apart from an initial calculation of behavioral d', the task performance (and its effect on neural activity) is largely unaddressed.

The reviewer makes several important points that we hope we addressed in the specific changes detailed below. Indeed, it is important to recognize the possibility that the specific stimuli involved in a task may interact with the effects of behavioral state and that variability in task performance should be considered as an important aspect of behavioral state.

Reviewer #1 (Recommendations For The Authors):

I have a few minor comments and criticisms:

(1) Figure 1c. The choice of low-contrast grey text (e.g. "Target vs. target" is unfortunate, especially when printed, and should be replaced (e.g. with dark grey).

We have edited the figure to use a higher contrast (dark grey). Thanks for catching this.

(2) Figure 2 and Supplementary Figure 3. I think some indication of error or significance is required in all panels. Without this, it's hard to interpret any of these panels.

Thank you for this feedback. Including significance here was clarifying and helps to strengthen our claim that state-dependent changes in neural activity were smaller and more diverse for single neurons than at the population level. We modified Figure 2b-c to indicate whether each neuron’s response to the target stimulus was significantly different than its response to the catch stimulus. The same test was performed in Supplementary Figure 3. Additionally, we added a statistical test in Figure 2d-e to indicate, for each pair of target/catch stimuli, whether discrimination (d-prime) changed significantly between active and passive conditions. Furthermore, we modified the text of the second paragraph under the results heading: “Diverse effects of task engagement on single neurons in primary and non-primary auditory cortex” to reference and interpret the results of these significance tests. The new text reads as follows (L. 121):

“Sound-evoked spiking activity was compared between active and passive states to study the impact of task engagement on sound representation. In both A1 and dPEG, responses to target and catch stimuli were significantly discriminable for a subset of single neurons (about 25% in both areas, Figure 2A-C, Supplemental Figures 3-5, bootstrap test). This supports the idea that stimulus identity can be decoded in both brain regions, regardless of task performance. However, the fact that the responses of most neurons in both brain areas could not significantly discriminate target vs. catch stimuli also highlights the diversity of sound encoding observed at the level of single neurons. The accuracy of catch vs. target discrimination for each neuron was quantified using neural d-prime, the z-scored difference in target minus catch spiking response for each neuron (Methods: Single neuron PSTHs and d-prime (Niwa et al., 2012a)). Task engagement was associated with significant changes in catch vs. target d-prime for roughly 10% of neurons in both A1 (40 / 481 neurons, bootstrap test) and dPEG (33 / 377 neurons, bootstrap test). This included neurons that both increased their discriminability and decreased their discriminability (Figure 2D-E). Thus, the effects of task engagement at the level of single neurons were relatively mild and inconsistent across the population; many neurons showed no significant change and of those that did, effects were bidirectional (Figure 2D-E).”

We also included an additional methods paragraph in the “Statistical tests” section to describe the bootstrapping procedure used for these significance tests (L. 644):

“The one exception to this general approach is in Figure 2, where we analyzed the sound discrimination abilities of single neurons. In this case, we computed p-values for each neuron and stimulus independently. First, for each neuron and catch vs. target stimulus pair, we measured d-prime (see Methods: Single neuron evoked activity and d-prime). We generated a null distribution of d-prime values for each neuron-stimulus pair, under each experimental condition by shuffling stimulus identity across trials before computing d-prime (100 resamples). A neuron was determined to have a significant d-prime for a given target vs. catch pair if its actual measured d-prime was greater than the 95th percentile of the null d-prime distribution. Second, for each neuron and catch vs. target stimulus pair, we tested if d-prime was significantly different between active and passive conditions. To test this, we followed a similar procedure as above, however, rather than shuffle stimulus identity, we shuffled active vs. passive trial labels. This allowed us to generate a null distribution of active vs. passive d-prime difference for each neuron and stimulus pair. A neuron was determined to have a significant change in d-prime between conditions if the actual Δ d-prime lay outside the 95% confidence interval of the null Δ d-prime distribution.”

For Figure 2a, we chose not to indicate significance on the figure to avoid clutter, since the significance for all neurons in the population are shown in panels b-c anyway. Additionally, the difference plot shown in panel a is in units of z-scores, which we believe already gives a raw sense of the significance of the target vs. catch response change per neuron in this example dataset.

(3) Figure 2 and Supplementary Figure 3. I would consider including some more examples as a Supplementary Figure (and perhaps combining Supp Fig 3 with Fig 2 as a main figure).

We found no significant or apparent difference in single-neuron properties between A1 and dPEG. Therefore, we decided it is not helpful to plot both A1 and PEG examples in the main text. However, we agree that the ability to see more examples of the raw data could be useful. Therefore, we compiled two supplementary figures (Supplementary Figures 4 and 5) that replicate Figure 2a for all datasets, encompassing A1 and PEG.

(4) Figure 2a and Supp Fig 3a. I was initially confused that the "delta-spk/sec (z-score)" values had themselves been z-scored, but now I think that they are simply the differences of the two left hand sub-panels. This could be made clear in the figure legend.

The figure legends have been modified to state the procedure for computing “delta-spk/sec” more clearly. Specifically, we added the following information to the legend (L. 141):

“Difference is computed as the z-scored response to the target minus the z-scored catch response (resulting in a difference shown in units of z-score).”

(5) Figure 2b-e and Supp Fig 3b-e. Indicate the time window over which the responses were measured, and the number of neurons.

Figure legends have been modified to include a sentence clearly stating the time window over which responses were measured. The number of neurons is also now included in the legend and on the figure itself. Furthermore, a brief description of the new statistical testing procedure has been added here (L. 144).

“Responses were defined as the total number of spikes recorded during the 300 ms of sound presentation (area between dashed lines in panel A). Neurons with a significantly different response to the catch vs. target stimulus are indicated in black and quantified on the respective figure panel.”

(6) Figure 2. "singe" should read "single"

Typo in figure label has been fixed.

(7) Line 144. Figure number is missing (Figure 3B-C).

The missing figure number has been added to the text.

(8) Figure 3. Again, the low-contrast grey should be replaced.

The low-contrast grey has been replaced with dark grey.

Reviewer #2 (Recommendations For The Authors):

This study really nicely compares the activity and effects on activity in two areas of the auditory cortex in respect to task-engagement; I think it is, for the most part, very well done.

A couple of specific recommendations:

(1) Although I understand 'inf dB' as the SNR, including the actual dB level used in the experiments, would be useful, especially in the case of the inf dB.

Thank you for this feedback. We agree that clarification about the overall sound level used here would be helpful. We have modified the methods section “Behavioral paradigm” to include the following sentence (L. 450):

“That is, the masking noise (and distractor stimuli) were always presented with an overall sound level of 60 dB SPL. Infinite (inf) dB trials corresponded to trials where the target tone was presented at 60 dB SPL without any masking noise present, 0 dB to trials where the target was 60 dB SPL, -5 dB to trials where the target was presented at 55 dB SPL etc.”

In addition, we have modified the main text (L. 82):

“Animals reported the occurrence of a target tone in a sequence of narrowband noise distractors by licking a piezo spout (Figure 1A, Methods: Behavioral paradigm, distractor stimulus sound level: 60 dB SPL). … We describe SNR as the overall SPL of the target relative to distractor noise level. Thus, an SNR of –5 dB corresponds to a target level of 55 dB SPL while an Inf dB SNR corresponds to a target tone presented without any masking noise.”

And Figure legend 1 now explicitly states the sound level used in the experiments (L. 104):

“Variable SNR was achieved by varying overall SPL of the target relative to the fixed (60 dB SPL) distractor noise, e.g., -5 dB SNR corresponds to a 55 dB SPL target with 60 dB SPL masking noise. Infinite (inf) dB SNR corresponds to a target tone presented in isolation (60 dB SPL).”

(2) I very much appreciate the attempt to disentangle task engagement from generalized arousal state, and specifically, addressing this through the use of pupillometry. However, by focusing the discussion of pupil dynamics solely on the arousal-state aspects of pupil size, the paper doesn't address the increasing evidence suggests that pupil size may fluctuate based upon a lot of other things, including perceptual events (see Kronemer et al, 2022 for a recent human paper; for auditory: Zekveld et al 2018 (review) and Montes-Lourido et al, 2021; but many many others, too). It would be nice to see either a bit more nuanced discussion of what pupil size may be indicating (easier), or analyzing the behavior in the context of pupil dynamics (a heavier lift).

This is a good point. We agree that it is worth mentioning these more nuanced aspects of cognition that may be reflected by pupil size. Therefore, we also analyzed pupil size in the context of behavioral performance (see Supplemental Figure 6) and added the following text to the results (L. 193).

“In addition to reflecting overall arousal level, pupil size has also been reported to reflect more nuanced cognitive variables such as, for example, listening effort (Zekveld et al., 2014). Furthermore, rodent data suggests that optimal sensory detection is associated with intermediate pupil size (McGinley et al., 2015), consistent with the hypothesis of an inverted-U relationship between arousal and behavioral performance (Zekveld et al., 2014). To determine if this pattern was true for the animals in our task, we measured the dynamics of pupil size in the context of behavioral performance. Across animals, task stimuli evoked robust pupil dilation that varied with trial outcome (Supplemental Figure 6b-c). Notably, pre-trial pupil size was significantly different between correct (hit and correct reject), hit, and miss trials (Supplemental Figure 6b-c), recapitulating the finding of an inverted-U relationship to performance in rodents (McGinley et al., 2015).  Since we focused only on correct trials in our decoding analysis, these outcome-dependent differences in pupil size are unlikely to contribute to the emergent decoding selectivity in dPEG.”

(3) I think it would make this paper shine that much more if behavioral performance were not subsumed into the overall label of task engagement. You've already established you have performance that varies as a function of SNR; I would love to see the neural d' and covariability related to the behavioral d' (in the comparisons where this is possible). I would also love to see a more direct measure of choice for those stimuli that show variable behavior (e.g., a choice probability analysis or something of the like would seem to be easily applied to the target SNRs of -5 and 0 dB); and compare task engaged activity of hits vs misses vs passive listening to those same stimuli. You discuss previous studies looking at choice-related/decision-related activity and draw parallels to this work-given that there is the opportunity with this data set to *directly* assess choice-related activity, the absence of such an analysis seems like a missed opportunity.

Thank you for this feedback. We agree that “task engagement” is not a unimodal state and that a more fine-grained analysis of task-engaged neural activity, according to behavioral choice, could be informative.

First, we would like to point out that in Figure 4 we did already compare behavioral d’ to delta neural d’. We found that the two were significantly correlated in dPEG, but not in A1. This suggests that task-dependent changes in stimulus decoding in dPEG, but not A1, are predictive of behavioral performance. This is consistent with the finding that task-relevant stimulus representations were selectively enhanced in dPEG, but not in A1.

Second, we added a choice decoding analysis to address whether auditory cortex represents the animal’s choice in our task. The results of this analysis are summarized in Supplemental Figure 8 and are discussed under the results section: “Behavioral performance is correlated with neural coding changes in non-primary auditory cortex only.” (L. 226):

“The previous analysis suggests that the task-dependent increase in stimulus information present in dPEG population activity is predictive of overall task performance. Next, we asked whether the population activity in either brain region was directly predictive of behavioral choice on single hit vs. miss trials. To do this, we conducted a choice probability analysis (Methods). We found that in both brain regions choice could be decoded well above chance level (Supplemental Figure 8). Choice information was present throughout the entire trial and did not increase during the target stimulus presentation. This suggests that the difference in population activity primarily reflects a cognitive state associated with the probability of licking on a given trial, or “impulsivity” rather than “choice.” This interpretation is consistent with our finding that baseline pupil size on each trial is predictive of trial outcome (Supplemental Figure 6b).”

To keep our decoding approach consistent throughout the manuscript, we followed the same approach for choice decoding as we did for stimulus decoding (perform dDR then calculate neural d-prime in the dimensionality reduced space). To make the results more interpretable, we converted choice d-prime to a choice probability (percent correctly decoded choices) using leave-one-out cross validation. (We note that d-prime and percent correct are very highly correlated statistics.) This is described in the methods as follows (L. 550):

“We performed a choice decoding analysis on hit vs. miss trials. We followed the same procedure as described above for stimulus decoding, where instead of a pair of stimuli our two classes to be decoded were “hit trial” vs. “miss trial”. That is, for each target stimulus we computed the optimal linear discrimination axis separating hit vs. miss trials (Abbott and Dayan, 1999) in the reduced dimensionality space identified with dDR (Heller and David, 2022). For the sake of interpretability with respect to previous work we reported choice probability as the percentage of correctly decoded trial outcomes rather than d-prime. Percent correct was calculated by projecting the population activity onto the optimal discrimination axis and using leave-one-out cross validation to measure the number of correct classifications.”

(4) It would also be interesting to look at population coding across sessions (although the point is taken that within a session allows the opportunity to assess covariability). Minorly self-servingly but very much related to the above point, Christison-Lagay et al, 2017 employed a similar detect-in-noise task, analyzed single neurons and population level activity, and looked at putative choice-related activity. The current study has the opportunity to expand on that kind of analysis that much more by looking across multiple sites vs within a given recording site; and compare across regions.

Thank you for highlighting this point, we agree that it is important. When studying population coding it is critical to consider the impact of covariability between neurons. Therefore, it is worthwhile to revisit our interpretations of prior results, e.g., Christison-Lagay et al, 2017, which studied population coding by combining neurons across different sessions, given that we now have access to simultaneously recorded population data.

First, we would like to point out that this was the primary motivation for our simulation analyses presented in Figure 5. Using simulations, we found that task-dependent gain modulation (which can be observed across sessions) was sufficient to explain our primary finding – selective enhancement in decoding of behaviorally relevant sound stimuli in dPEG.

Second, to address the question about how covariability affects choice-related information in auditory cortex and compare our findings with prior studies, we performed the same set of simulations for choice probability analysis. We found that, again, choice-dependent gain modulation was sufficient to explain our findings. That is, simulations with hit- vs. miss-dependent gain changes, but fixed covariability, closely mirrored the choice probability we observed in the raw data. An additional simulation where covariability between all neurons was set to zero also recapitulated our findings in the raw data. Collectively, this suggests that covariability does not play a significant role in shaping the choice information present in A1 and dPEG during this task. We have added the following text to the manuscript to summarize this finding (L. 293):

“Finally, we used the same simulation approach to determine what aspects of population activity carry the “choice” related information we observed in A1 and dPEG (Figure 4 – figure supplement 1). Similar to our findings for stimulus decoding, we found that gain modulation alone was sufficient to recapitulate the choice information present in the raw data for this task. This helps frame prior work that pooled neurons across sessions to study population coding of choice in similar auditory discrimination tasks (Christison-Lagay et al, 2017).”

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study introduces and validates the Cyclic Homogeneous Oscillation (CHO) detection method to precisely determine the duration, location, and fundamental frequency of non-sinusoidal neural oscillations. Traditional spectral analysis methods face challenges in distinguishing the fundamental frequency of non-sinusoidal oscillations from their harmonics, leading to potential inaccuracies. The authors implement an underexplored approach, using the auto-correlation structure to identify the characteristic frequency of an oscillation. By combining this strategy with existing time-frequency tools to identify when oscillations occur, the authors strive to solve outstanding challenges involving spurious harmonic peaks detected in time-frequency representations. Empirical tests using electrocorticographic (ECoG) and electroencephalographic (EEG) signals further support the efficacy of CHO in detecting neural oscillations.

Response:  We thank the reviewer for recognizing the strengths of our method in this encouraging review and for the opportunity to further improve and finalize our manuscript.

Strengths:

(1) The paper puts an important emphasis on the 'identity' question of oscillatory identification. The field primarily identifies oscillations through frequency, space (brain region), and time (length, and relative to task or rest). However, more tools that claim to further characterize oscillations by their defining/identifying traits are needed, in addition to data-driven studies about what the identifiable traits of neural oscillations are beyond frequency, location, and time. Such tools are useful for potentially distinguishing between circuit mechanistic generators underlying signals that may not otherwise be distinguished. This paper states this problem well and puts forth a new type of objective for neural signal processing methods.

Response:  We sincerely appreciate this encouraging summary of the objective of our manuscript.

(2) The paper uses synthetic data and multimodal recordings at multiple scales to validate the tool, suggesting CHO's robustness and applicability in various real-data scenarios. The figures illustratively demonstrate how CHO works on such synthetic and real examples, depicting in both time and frequency domains. The synthetic data are well-designed, and capable of producing transient oscillatory bursts with non-sinusoidal characteristics within 1/f noise. Using both non-invasive and invasive signals exposes CHO to conditions which may differ in extent and quality of the harmonic signal structure. An interesting followup question is whether the utility demonstrated here holds for MEG signals, as well as source-reconstructed signals from non-invasive recordings.

Response:  We thank the reviewer for this excellent suggestion.  Indeed, our next paper will focus on applying our CHO method to signals that were source-reconstructed from non-invasive recordings (e.g., MEG and EEG) to extract their periodic activity.

(3) This study is accompanied by open-source code and data for use by the community.

Response:  We thank the reviewer for recognizing our effort to widely disseminate our method to the broader community.

Weaknesses:

(1) Due to the proliferation of neural signal processing techniques that have been designed to tackle issues such as harmonic activity, transient and event-like oscillations, and non-sinusoidal waveforms, it is naturally difficult for every introduction of a new tool to include exhaustive comparisons of all others. Here, some additional comparisons may be considered for the sake of context, a selection of which follows, biased by the previous exposure of this reviewer. One emerging approach that may be considered is known as state-space models with oscillatory and autoregressive components (Matsuda 2017, Beck 2022). State-space models such as autoregressive models have long been used to estimate the auto-correlation structure of a signal. State-space oscillators have recently been applied to transient oscillations such as sleep spindles (He 2023). Therefore, state-space oscillators extended with auto-regressive components may be able to perform the functions of the present tool through different means by circumventing the need to identify them in time-frequency. Another tool that should be mentioned is called PAPTO (Brady 2022). Although PAPTO does not address harmonics, it detects oscillatory events in the presence of 1/f background activity. Lastly, empirical mode decomposition (EMD) approaches have been studied in the context of neural harmonics and nonsinusoidal activity (Quinn 2021, Fabus 2022). EMD has an intrinsic relationship with extrema finding, in contrast with the present technique. In summary, the existence of methods such as PAPTO shows that researchers are converging on similar approaches to tackle similar problems. The existence of time-domain approaches such as state-space oscillators and EMD indicates that the field of timeseries analysis may yield even more approaches that are conceptually distinct and may theoretically circumvent the methodology of this tool.

Response:  We thank the reviewer for this valuable insight.  In our manuscript, we acknowledge emerging approaches that employ state-space models or EMD for time-frequency analysis.  However, it's crucial to clarify that the primary focus in our study is on the detection and identification of the fundamental frequency, as well as the onset/offset of non-sinusoidal neural oscillations.  Thus, our emphasis lies specifically on these aspects.  We hope that future studies will use our methods as the basis to develop better methods for time-frequency analysis that will lead to a deeper understanding of harmonic structures.  

Our Limitation section is addressing this issue.  Specifically, we recognize that a more sophisticated time-frequency analysis could contribute to improved sensitivity and that the core claim of our study is centered around the concept of increasing specificity in the detection of non-sinusoidal oscillations.  We hope that future studies will use this as a basis for improving time-frequency analysis in general.  Notably, our open-source code will greatly enable these future studies in this endeavor.  Specifically, in the first step of our algorithm, the timefrequency estimation can be replaced with any other preferred time-frequency analysis, such as state-space models, EMD, Wavelet transform, Gabor transform, and Matching Pursuit. 

For our own follow-up study, we plan to conduct a thorough review and comparison of emerging approaches employing state-space models or EMD for time-frequency analysis.  In this study, we aim to identify which approach, including the six methods mentioned by the reviewer (Matsuda 2017, Beck 2022, He 2023, Brady 2022, Quinn 2021, and Fabus 2022), can maximize the estimation of the fundamental frequency of non-sinusoidal neural oscillations using CHO.  The insights provided by the reviewer are appreciated, and we will carefully consider these aspects in our follow-up study.  

In the revision of this manuscript, we are setting the stage for these future studies.  Specifically, we added a discussion paragraph within the Limitation section about the state-space model, and EMD approaches:

“However, because our CHO method is modular, the FFT-based time-frequency analysis can be replaced with more sophisticated time-frequency estimation methods to improve the sensitivity of neural oscillation detection.  Specifically, a state-space model (Matsuda 2017, Beck 2022, He 2023, Brady 2022) or empirical mode decomposition (EMD, Quinn 2021, Fabus 2022) may improve the estimation of the auto-correlation of the harmonic structure underlying nonsinusoidal oscillations.  Furthermore, a Gabor transform or matching pursuit-based approach may improve the onset/offset detection of short burst-like neural oscillations (Kus 2013 and Morales 2022).”

(2) The criteria that the authors use for neural oscillations embody some operating assumptions underlying their characteristics, perhaps informed by immediate use cases intended by the authors (e.g., hippocampal bursts). The extent to which these assumptions hold in all circumstances should be investigated. For instance, the notion of consistent auto-correlation breaks down in scenarios where instantaneous frequency fluctuates significantly at the scale of a few cycles. Imagine an alpha-beta complex without harmonics (Jones 2009). If oscillations change phase position within a timeframe of a few cycles, it would be difficult for a single peak in the auto-correlation structure to elucidate the complex time-varying peak frequency in a dynamic fashion. Likewise, it is unclear whether bounding boxes with a pre-specified overlap can capture complexes that maneuver across peak frequencies.

Response:  We thank the reviewer for this valuable insight into the methodological limitations in the detection of neural oscillations that exhibit significant fluctuations in their instantaneous frequency.  Indeed, our CHO method is also limited in the ability to detect oscillations with fluctuating instantaneous frequencies.  This is because CHO uses an auto-correlation-based approach to detect neural oscillations that exhibit two or more cycles.  If oscillations change phase position within a timeframe of a few cycles, CHO cannot detect the oscillation because the periodicity is not expressed within the auto-correlation.  This limitation can be partially overcome by relaxing the detection threshold (see Line 30 of Algorithm 1 in the revised manuscript) for the auto-correlation analysis.  However, relaxing the detection threshold, in consequence, increases the probability of detecting other aperiodic activity as well. To clarify how CHO determines the periodicity of oscillations, and to educate the reader about the tradeoff between detecting oscillations with fluctuating instantaneous frequencies and avoiding detecting other aperiod activity, we have added pseudo code and a new subsection in the Methods.

Author response table 1.

Algorithm 1

A new subsection titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO”.

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also reduces sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1.  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

(3) Related to the last item, this method appears to lack implementation of statistical inferential techniques for estimating and interpreting auto-correlation and spectral structure. In standard practice, auto-correlation functions and spectral measures can be subjected to statistical inference to establish confidence intervals, often helping to determine the significance of the estimates. Doing so would be useful for expressing the likelihood that an oscillation and its harmonic has the same autocorrelation structure and fundamental frequency, or more robustly identifying harmonic peaks in the presence of spectral noise. Here, the authors appear to use auto-correlation and time-frequency decomposition more as a deterministic tool rather than an inferential one. Overall, an inferential approach would help differentiate between true effects and those that might spuriously occur due to the nature of the data. Ultimately, a more statistically principled approach might estimate harmonic structure in the presence of noise in a unified manner transmitted throughout the methodological steps.

Response:  We thank the reviewer for sharing this insight on further enhancing our method.  Indeed, CHO does not make use of statistical inferential statistics to estimate and interpret the auto-correlation and underlying spectral structure of the neural oscillation.  Implementing this approach within CHO would require calculating phase-phase coupling across all cross-frequency bands and bounding boxes.  However, as mentioned in the introduction section and Figure 1GL, phase-phase coupling analysis cannot fully ascertain whether the oscillations are phaselocked and thus are harmonics or, indeed, independent oscillations.  This ambiguity, combined with the exorbitant computational complexity of the entailed permutation test and the requirement to perform the analysis across all cross-frequency bands, channels, and trials, makes phase-phase coupling impracticable in determining the fundamental frequency of neural oscillations in real-time and, thus, the use in closed-loop neuromodulation applications.  Thus, within our study, we prioritized determining the fundamental frequency without considering the structure of harmonics.  

An inferential approach can be implemented by adjusting the significance threshold that selects positive peaks within the auto-correlation of the signal.  Currently, this threshold is set to represent the approximate confidence bounds of the periodicity of the fundamental frequency.  To clarify this issue, we added additional pseudo code and a new subsection, titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO,” in the Methods section.

In future studies, we will investigate the harmonic structure of neural oscillations based on a large data set.  This exploration will help us understand how non-sinusoidal properties may influence the harmonic structure.  Your input is highly appreciated, and we will diligently incorporate these considerations into our research.

See Author response table 1.

A new subsection titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO”.

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also reduces sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1.  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

(4) As with any signal processing method, hyperparameters and their ability to be tuned by the user need to be clearly acknowledged, as they impact the robustness and reproducibility of the method. Here, some of the hyperparameters appear to be: a) number of cycles around which to construct bounding boxes and b) overlap percentage of bounding boxes for grouping. Any others should be highlighted by the authors and clearly explained during the course of tool dissemination to the community, ideally in tutorial format through the Github repository.

Response:  We thank the reviewer for this helpful suggestion.  In response, we added a new subsection that describes the hyper-parameters of CHO as follows:

A new subsection named “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO”.

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also reduces sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1.  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

(5) Most of the validation demonstrations in this paper depict the detection capabilities of CHO. For example, the authors demonstrate how to use this tool to reduce false detection of oscillations made up of harmonic activity and show in simulated examples how CHO performs compared to other methods in detection specificity, sensitivity, and accuracy. However, the detection problem is not the same as the 'identity' problem that the paper originally introduced CHO to solve. That is, detecting a non-sinusoidal oscillation well does not help define or characterize its non-sinusoidal 'fingerprint'. An example problem to set up this question is: if there are multiple oscillations at the same base frequency in a dataset, how can their differing harmonic structure be used to distinguish them from each other? To address this at a minimum, Figure 4 (or a followup to it) should simulate signals at similar levels of detectability with different 'identities' (i.e. different levels and/or manifestations of harmonic structure), and evaluate CHO's potential ability to distinguish or cluster them from each other. Then, does a real-world dataset or neuroscientific problem exist in which a similar sort of exercise can be conducted and validated in some way? If the "what" question is to be sufficiently addressed by this tool, then this type of task should be within the scope of its capabilities, and validation within this scenario should be demonstrated in the paper. This is the most fundamental limitation at the paper's current state.

Response: Thank you for your insightful suggestion; we truly appreciate it. We recognize that the 'identity' problem requires further studies to develop appropriate methods. Our current approach does not fully address this issue, as it may detect asymmetric non-sinusoidal oscillations with multiple harmonic peaks, without accounting for different shapes of nonsinusoidal oscillations.

The main reason we could not fully address the “identity” problem results from the general absence of a defined ground truth, i.e., data for which we know the harmonic structure. To overcome this barrier, we would need datasets from well-characterized cognitive tasks or neural disorders.  For example, Cole et al. 2017 showed that the harmonic structure of beta oscillations can explain the degree of Parkinson’s disease, and Hu et al. 2023 showed that the number of harmonic peaks can localize the seizure onset zone. Future studies could use the data from these two studies to study whether CHO can distinguish different harmonic structures of pathological neural oscillations.

In this paper, we showed the basic identity of neural oscillations, encompassing elements such as the fundamental frequency and onset/offset. Your valuable insights contribute significantly to our ongoing efforts, and we appreciate your thoughtful consideration of these aspects. In response, we added a new paragraph in the Limitation of the discussion section as below:

“Another limitation of this study is that it does not assess the harmonic structure of neural oscillations. Thus, CHO cannot distinguish between oscillations that have the same fundamental frequency but differ in their non-sinusoidal properties.  This limitation stems from the objective of this study, which is to identify the fundamental frequency of non-sinusoidal neural oscillations.  Overcoming this limitation requires further studies to improve CHO to distinguish between different non-sinusoidal properties of pathological neural oscillations.  The data that is necessary for these further studies could be obtained from the wide range of studies that have linked the harmonic structures in the neural oscillations to various cognitive functions (van Dijk et al., 2010; Schalk, 2015; Mazaheri and Jensen, 2008) and neural disorders (Cole et al., 2017; Jackson et al., 2019; Hu et al., 2023). For example, Cole et al. 2017 showed that a harmonic structure of beta oscillations can explain the degree of Parkinson’s disease, and Hu et al. 2023 showed the number of harmonic peaks can localize the seizure onset zone. “

References:

Beck AM, He M, Gutierrez R, Purdon PL. An iterative search algorithm to identify oscillatory dynamics in neurophysiological time series. bioRxiv. 2022. p. 2022.10.30.514422.

doi:10.1101/2022.10.30.514422

Brady B, Bardouille T. Periodic/Aperiodic parameterization of transient oscillations (PAPTO)Implications for healthy ageing. Neuroimage. 2022;251: 118974.

Fabus MS, Woolrich MW, Warnaby CW, Quinn AJ. Understanding Harmonic Structures Through Instantaneous Frequency. IEEE Open J Signal Process. 2022;3: 320-334.

Jones SR, Pritchett DL, Sikora MA, Stufflebeam SM, Hämäläinen M, Moore CI. Quantitative analysis and biophysically realistic neural modeling of the MEG mu rhythm: rhythmogenesis and modulation of sensory-evoked responses. J Neurophysiol. 2009;102: 3554-3572.

He M, Das P, Hotan G, Purdon PL. Switching state-space modeling of neural signal dynamics. PLoS Comput Biol. 2023;19: e1011395.

Matsuda T, Komaki F. Time Series Decomposition into Oscillation Components and Phase Estimation. Neural Comput. 2017;29: 332-367.

Quinn AJ, Lopes-Dos-Santos V, Huang N, Liang W-K, Juan C-H, Yeh J-R, et al. Within-cycle instantaneous frequency profiles report oscillatory waveform dynamics. J Neurophysiol. 2021;126: 1190-1208.

Reviewer #2 (Public Review):

Summary:

A new toolbox is presented that builds on previous toolboxes to distinguish between real and spurious oscillatory activity, which can be induced by non-sinusoidal waveshapes. Whilst there are many toolboxes that help to distinguish between 1/f noise and oscillations, not many tools are available that help to distinguish true oscillatory activity from spurious oscillatory activity induced in harmonics of the fundamental frequency by non-sinusoidal waveshapes. The authors present a new algorithm which is based on autocorrelation to separate real from spurious oscillatory activity. The algorithm is extensively validated using synthetic (simulated) data, and various empirical datasets from EEG, intracranial EEG in various locations and domains (i.e. auditory cortex, hippocampus, etc.).

Strengths:

Distinguishing real from spurious oscillatory activity due to non-sinusoidal waveshapes is an issue that has plagued the field for quite a long time. The presented toolbox addresses this fundamental problem which will be of great use for the community. The paper is written in a very accessible and clear way so that readers less familiar with the intricacies of Fourier transform and signal processing will also be able to follow it. A particular strength is the broad validation of the toolbox, using synthetic, scalp EEG, EcoG, and stereotactic EEG in various locations and paradigms.

Weaknesses:

At many parts in the results section critical statistical comparisons are missing (e.g. FOOOF vs CHO). Another weakness concerns the methods part which only superficially describes the algorithm. Finally, a weakness is that the algorithm seems to be quite conservative in identifying oscillatory activity which may render it only useful for analysing very strong oscillatory signals (i.e.

alpha), but less suitable for weaker oscillatory signals (i.e. gamma).

Response: We thank Reviewer #2 for the assistance in improving this manuscript.  In the revised manuscript, we have added the missing statistical comparisons, detailed pseudo code, and a subsection that explains the hyper-parameters of CHO.  We also recognize the limitations of CHO in detecting gamma oscillations.  While our results demonstrate beta-band oscillations in ECoG and EEG signals (see Figures 5 and 6), we had no expectation to find gamma-band oscillations during a simple reaction time task.  This is because of the general absence of ECoG electrodes over the occipital cortex, where such gamma-band oscillations may be found. 

Nevertheless, our CHO method should be able to detect gamma-band oscillations.  This is because if there are gamma-band oscillations, they will be reflected as a bump over the 1/f fit in the power spectrum, and CHO will detect them.  We apologize for not specifying the frequency range of the synthetic non-sinusoidal oscillations.  The gamma band was also included in our simulation. We added the frequency range (1-40 Hz) of the synthetic nonsinusoidal oscillations in the subsection, the caption of Figure 4, and the result section.

Reviewer #1 (Recommendations For The Authors):

(1) The example of a sinusoidal neural oscillation in Fig 1 seems to still exhibit a great deal of nonsinusoidal behavior. Although it is largely symmetrical, it has significant peak-trough symmetry as well as sharper peak structure than typical sinusoidal activity. Nevertheless, it has less harmonic structure than the example on the left. A more precisely-stated claim might be that non-sinusoidal behavior is not the distinguishing characteristic between the two, but rather the degree of harmonic structure.

Response: We are grateful for this thoughtful observation. In response, we now recognize that the depicted example showcases pronounced peak-trough symmetry and sharpness, characteristics that might not be typically associated with sinusoidal behavior. We now better understand that the key differentiator between the examples lies not only in their nonsinusoidal behavior but also in their harmonic structure. To reflect this better understanding, we have refined our manuscript to more accurately articulate the differences in harmonic structure, in accordance with your suggestion. Specifically, we revised the caption of Fig 1 in the manuscript as follows:

The caption of the Fig 1G-L.

“We applied the same statistical test to a more sinusoidal neural oscillation (G). Since this neural oscillation more closely resembles a sinusoidal shape, it does not exhibit any prominent harmonic peaks in the alpha and beta bands within the power spectrum (H) and time-frequency domain (I).  Consequently, our test found that the phase of the theta-band and beta-band oscillations were not phase-locked (J-L).  Thus, this statistical test suggests the absence of a harmonic structure.”

(2) The statement "This suggests that most of the beta oscillations

detected by conventional methods are simply harmonics of the predominant asymmetric alpha oscillation." is potentially overstated. It is important to constrain this statement to the auditory cortex in which the authors conduct the validation, because true beta still exists elsewhere. The same goes for the beta-gamma claim later on. In general, use of "may be" is also more advisable than the definitive "are".

Response: We thank the reviewer for this thoughtful feedback. To avoid the potential overstatement of our findings we revised our statement on beta oscillations in the manuscript as follows:

Discussion:

“This suggests that most of the beta oscillations detected by conventional methods within auditory cortex may be simply harmonics of the predominant asymmetric alpha oscillation.”

Reviewer #2 (Recommendations For The Authors):

All my concerns are medium to minor and I list them as they appear in the manuscript. I do not suggest new experiments or a change in the results, instead I focus on writing issues only.

a) Line 50: A reference to the seminal paper by Klimesch et al (2007) on alpha oscillations and inhibition would seem appropriate here.

Response: We added the reference to Klimesch et al. (2007).

b) Figure 4: It is unclear which length for the simulated oscillations was used to generate the data in panels B-G.

Response: We generated oscillations that were 2.5 cycles in length and 1-3 seconds in duration. We added this information to the manuscript as follows.

Figure 4:

“We evaluated CHO by verifying its specificity, sensitivity, and accuracy in detecting the fundamental frequency of non-sinusoidal oscillatory bursts (2.5 cycles, 1–3 seconds long) convolved with 1/f noise.”

Results (page 5, lines 163-165):

“To determine the specificity and sensitivity of CHO in detecting neural oscillations, we applied CHO to synthetic non-sinusoidal oscillatory bursts (2.5 cycles, 1–3 seconds long) convolved with 1/f noise, also known as pink noise, which has a power spectral density that is inversely proportional to the frequency of the signal.”

Methods (page 20, lines 623-626):

“While empirical physiological signals are most appropriate for validating our method, they generally lack the necessary ground truth to characterize neural oscillation with sinusoidal or non-sinusoidal properties. To overcome this limitation, we first validated CHO on synthetic nonsinusoidal oscillatory bursts (2.5 cycles, 1–3 seconds long) convolved with 1/f noise to test the performance of the proposed method.”

c) Figure 5 - supplements: Would be good to re-organize the arrangement of the plots on these figures to facilitate the comparison between Foof and CHO (i.e. by presenting for each participant FOOOF and CHO together).

Response: We combined Figure 5-supplementary figures 1 and 2 into Figure 5-supplementary figure 1, Figure 6-supplementary figures 1 and 2 into Figure 6-supplementary figure 1, and Figure 8-supplementary figures 1 and 2 into Figure 8-supplementary figure 1. 

Author response image 1.

Figure 5-supplementary figure 1:

Author response image 2.

Figure 6-supplementary figure 1:

Author response image 3.

Figure 8-supplementary figure 1:

d) Statistics: Almost throughout the results section where the empirical results are described statistical comparisons are missing. For instance, in lines 212-213 the statement that CHO did not detect low gamma while FOOOF did is not backed up by the appropriate statistics. This issue is also evident in all of the following sections (i.e. EEG results, On-offsets of oscillations, SEEG results, Frequency and duration of oscillations). I feel this is probably the most important point that needs to be addressed.

Response: We added statistical comparisons to Figure 5 (ECoG), 6 (EEG), and the results section as follows.

Author response image 4.

Validation of CHO in detecting oscillations in ECoG signals. A. We applied CHO and FOOOF to determine the fundamental frequency of oscillations from ECoG signals recorded during the pre-stimulus period of an auditory reaction time task. FOOOF detected oscillations primarily in the alpha- and beta-band over STG and pre-motor area.  In contrast, CHO also detected alpha-band oscillations primarily within STG, and more focal beta-band oscillations over the pre-motor area, but not STG. B. We investigated the occurrence of each oscillation within defined cerebral regions across eight ECoG subjects. The horizontal bars and horizontal lines represent the median and median absolute deviation (MAD) of oscillations occurring across the eight subjects. An asterisk (*) indicates statistically significant differences in oscillation detection between CHO and FOOOF (Wilcoxon rank-sum test, p<0.05 after Bonferroni correction).”

Author response image 5.

Validation of CHO in detecting oscillations in EEG signals. A. We applied CHO and FOOOF to determine the fundamental frequency of oscillations from EEG signals recorded during the pre-stimulus period of an auditory reaction time task.  FOOOF primarily detected alpha-band oscillations over frontal/visual areas and beta-band oscillations across all areas (with a focus on central areas). In contrast, CHO detected alpha-band oscillations primarily within visual areas and detected more focal beta-band oscillations over the pre-motor area, similar to the ECoG results shown in Figure 5. B. We investigated the occurrence of each oscillation within the EEG signals across seven subjects. An asterisk (*) indicates statistically significant differences in oscillation detection between CHO and FOOOF (Wilcoxon rank-sum test, p<0.05 after Bonferroni correction). CHO exhibited lower entropy values of alpha and beta occurrence than FOOOF across 64 channels. C. We compared the performance of FOOO and CHO in detecting oscillation across visual and pre-motor-related EEG channels. CHO detected more alpha and beta oscillations in visual cortex than in pre-motor cortex. FOOOF detected alpha and beta oscillations in visual cortex than in pre-motor cortex.

We added additional explanations of our statistical results to the “Electrocorticographic (ECoG) results” and “Electroencephalographic (EEG) results” sections.

“We compared neural oscillation detection rates between CHO and FOOOF across eight ECoG subjects.  We used FreeSurfer to determine the associated cerebral region for each ECoG location. Each subject performed approximately 400 trials of a simple auditory reaction-time task.  We analyzed the neural oscillations during the 1.5-second-long pre-stimulus period within each trial. CHO and FOOOF demonstrated statistically comparable results in the theta and alpha bands despite CHO exhibiting smaller median occurrence rates than FOOOF across eight subjects. Notably, within the beta band, excluding specific regions such as precentral, pars opercularis, and caudal middle frontal areas, CHO's beta oscillation detection rate was significantly lower than that of FOOOF (Wilcoxon rank-sum test, p < 0.05 after Bonferroni correction). This suggests comparable detection rates between CHO and FOOOF in premotor and Broca's areas, while the detection of beta oscillations by FOOOF in other regions, such as the temporal area, may represent harmonics of theta or alpha, as illustrated in Figure 5A and B. Furthermore, FOOOF exhibited a higher sensitivity in detecting delta, theta, and low gamma oscillations overall, although both CHO and FOOOF detected only a limited number of oscillations in these frequency bands.”

“We assessed the difference in neural oscillation detection performance between CHO and FOOOF across seven EEG subjects.  We used EEG electrode locations according to the 10-10 electrode system and assigned each electrode to the appropriate underlying cortex (e.g., O1 and O2 for the visual cortex). Each subject performed 200 trials of a simple auditory reaction-time task.  We analyzed the neural oscillations during the 1.5-second-long pre-stimulus period. In the alpha band, CHO and FOOOF presented statistically comparable outcomes. However, CHO exhibited a greater alpha detection rate for the visual cortex than for the pre-motor cortex, as shown in Figures 6B and C. The entropy of CHO's alpha oscillation occurrences (3.82) was lower than that of FOOOF (4.15), with a maximal entropy across 64 electrodes of 4.16. Furthermore, in the beta band, CHO's entropy (4.05) was smaller than that of FOOOF (4.15). These findings suggest that CHO may offer a more region-specific oscillation detection than FOOOF.

As illustrated in Figure 6C, CHO found fewer alpha oscillations in pre-motor cortex (FC2 and FC4) than in occipital cortex (O1 and O2), while FOOOF found more beta oscillations occurrences in pre-motor cortex (FC2 and FC4) than in occipital cortex. However, FOOOF found more alpha and beta oscillations in visual cortex than in pre-motor cortex.

Consistent with ECoG results, FOOOF demonstrated heightened sensitivity in detecting delta, theta, and low gamma oscillations. 

Nonetheless, both CHO and FOOOF identified only a limited number of oscillations in delta and theta frequency bands.

Contrary to the ECoG results, FOOOF found more low gamma oscillations in EEG subjects than in ECoG subjects.”

e) Line 248: The authors find an oscillatory signal in the hippocampus with a frequency at around 8 Hz, which they refer to as alpha. However, several researchers (including myself) may label this fast theta, according to the previous work showing the presence of fast and slow theta oscillations in the human hippocampus (https://pubmed.ncbi.nlm.nih.gov/21538660/, https://pubmed.ncbi.nlm.nih.gov/32424312/).

Response: We replaced “alpha” with “fast theta” in the figure and text. We added a citation for Lega et al. 2012.

f) Line 332: It could also be possible that the auditory alpha rhythms don’t show up in the EEG because a referencing method was used that was not ideal for picking it up. In general, re-referencing is an important preprocessing step that can make the EEG be more susceptible to deep or superficial sources and that should be taken into account when interpreting the data.

Response: We re-referenced our signals using a common median reference (see Methods section). After close inspection of our results, we found that the EEG topography shown in Figure 6 did not show the auditory alpha oscillation because the alpha power of visual locations greatly exceeded that of those locations that reflect oscillations in the auditory cortex. Further, while our statistical analysis shows that CHO detected auditory alpha oscillations, this analysis also shows that CHO detected significantly more visual alpha oscillations.

g) Line 463: It seems that the major limitation of the algorithm lies in its low sensitivity which is discussed by the authors. The authors seem to downplay this a bit by saying that the algorithm works just fine at SNRs that are comparable to alpha oscillations. However, alpha is the strongest single in human EEG which may make the algorithm less suitable for picking up less prominent oscillatory signals, i.e. gamma, theta, ripples, etc. Is CHO only seeing the ‘tip of the iceberg’?

Response:  We performed the suggested analysis. For the theta band, this analysis generated convincing statistical results for ECoG signals (Figures 5, 6, and the results section). For theta oscillation detection, we found no statistical difference between CHO and FOOOF.  Since FOOOF has a high sensitivity even under SNRs (as shown in our simulation), our analysis suggests that CHO and FOOOF should perform equally well in the detection of theta oscillation, even when the theta oscillation amplitude is small.

To validate the ability of CHO to detect oscillations in high-frequency bands (> 40Hz), such as gamma oscillations and ripples, our follow-up study is applying CHO in the detection of highfrequency oscillations (HFOs) in electrocorticographic signals recorded during seizures.  To this end, our follow-up study analyzed 26 seizures from six patients.  In this analysis, CHO showed similar sensitivity and specificity as the epileptogenicity index (EI), which is the most commonly used method to detect seizure onset times and zones. The results of this follow-up study were presented at the American Epilepsy Society Meeting in December of 2023, and we are currently preparing a manuscript for submission to a peer-reviewed journal. 

In this study, we want to investigate the performance of CHO in detecting the most prominent neural oscillations (e.g., alpha and beta). Future studies will investigate the performance of  CHO in detecting more difficult to observe oscillations (delta in sleep stages, theta in the hippocampus during memory tasks, and high-frequency oscillation or ripples in seizure or interictal data. 

h) Methods: The methods section, especially the one describing the CHO algorithm, is lacking a lot of detail that one usually would like to see in order to rebuild the algorithm themselves. I appreciate that the code is available freely, but that does not, in my opinion, relief the authors of their duty to describe in detail how the algorithm works. This should be fixed before publishing.

Response: We now present pseudo code to describe the algorithms within the new subsection on the hyper-parameterization of CHO.

See Author response table 1.

A new subsection titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO.”

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four time windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1 (the approximate 68% confidence bounds).  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this study, the authors investigate the tolerance of aminoglycosides in E. coli mutants deleted in the Krebs cycle and respiratory chain enzymes. The motivation for this study is unclear. Transport of aminoglycosides is pmf-dependent, as the authors correctly note, and knocking out energy-producing components leads to tolerance of aminoglycosides, this has been well established. In S. aureus, clinically relevant "small colony" strains selected for in the course of therapy with aminoglycosides acquire null mutations in the biosynthesis of heme or ubiquinone, and have been studied in detail. In E. coli, such knockouts have not been reported in clinical isolates, probably due to severe fitness costs.

Response: We sincerely appreciate the time and consideration the reviewer dedicated to evaluating our manuscript. It's important to highlight that while the transport of aminoglycosides is PMF-dependent, recent studies underscore the potential role of metabolic mutations in antibiotic tolerance, a facet that warrants further investigation. For instance, the study by Henimann’s and Michiels' groups explored genomic changes in E. coli strains (including uropathogenic UTI89 strains) subjected to daily antibiotic exposure (Van den Bergh et al., 2022). Notably, mutations predominantly occurred in genes of the nuo operon, a key component of E. coli energy metabolism, suggesting a link between metabolic adaptations and antibiotic tolerance. Furthermore, the research by Collin's group revealed previously unrecognized genes related to central metabolism (e.g., icd, gltD, sucA) that contribute to antibiotic resistance in E. coli cells exposed to multiple antibiotics, including aminoglycosides (Lopatkin et al., 2021). These findings are corroborated by the presence of similar mutations in clinical E. coli pathogens, as evidenced by the analysis of a large library of 7243 E. coli genomes from NCBI Pathogen Detection (Lopatkin et al., 2021). The clinical relevance of metabolic mutations in antibiotic tolerance is increasingly recognized, yet their underlying mechanisms remain enigmatic. Therefore, elucidating the role of metabolic pathways in conferring antibiotic tolerance is highly critical. We have updated the introduction to clearly convey our motivation in this study (see page 4).

At the same time, single-cell analysis has shown that individual cells with a decrease in the expression of Krebs cycle enzymes are tolerant of antibiotics and have lower ATP (Manuse et al., PLoS Biol 19: e3001194). The authors of the study under review report that knocking out ICD, isocitrate dehydrogenase that catalyzes the rate-limiting step in the Krebs cycle, has little effect on aminoglycoside tolerance and actually leads to an increase in the level of ATP over time. This observation does not seem to make much sense and contradicts previous reports, specifically that E. coli ICD is tolerant of antibiotics and, not surprisingly, produces Less ATP (Kabir and Shimizu, Appl Micro-biol Biotechnol. 2004; 65(1):84-96; Manuse et al., PLoS Biol 19: e3001194). Mutations in other Krebs cycle enzymes, unlike ICD, do lead to a dramatic increase in tolerance of aminoglycosides according to the paper under review. This is all very confusing.

Response: Although our data cannot be directly compared to that of Kabir and Shimizu (Mohiuddin Kabir and Shimizu, 2004), due to the utilization of entirely different experimental procedures and measurement techniques, we can draw some parallels to the study conducted by Lewis’ group (Manuse et al., 2021), despite certain differences in experimental protocols. Furthermore, the reviewer has made strong assertions regarding our manuscript based on the findings of Lewis’ group. Thus, we believe it's pertinent to expand our response regarding that study.

In the study of Lewis’ group, bacterial cells were inoculated at a ratio of 1:100 into LB medium from an overnight culture (approximately 16 hours). Subsequently, the cultures were incubated at 37°C for approximately 2 hours, and ATP levels were measured using the BacTiter Glo kit (Promega, Madison, WI, USA). ATP levels were then normalized to cell density, determined through optical density measurements, and represented on a linear diagram. As demonstrated in Supplementary Figure S1c of their paper, there was a 10-15% reduction in normalized ATP levels in the icd mutant compared to the wild type. In our experiments, cells were grown for 24 hours in overnight cultures, diluted 100-fold in fresh media, and ATP levels were measured at 3, 4, 5, and 6 hours using the same kit. ATP levels were normalized to cell counts quantified by flow cytometry. Upon analyzing our data of the icd mutant for around 3 hours (the time point closest to that of the study of Lewis’ group), we observed a reduction of approximately 15-20% (without statistical significance) in the icd mutant compared to the wild-type (see raw data, linear plot, and logarithmic plot below; Author response image 1), which aligns with the findings of Lewis’ group.

We further investigated the gentamicin tolerance of both wild-type and icd mutant strains of E. coli BW25113 (Author response image 2). Our findings indicate that the increased sensitivity of the icd mutant of the MG1655 strain to gentamicin is similar to the observation in the other E. coli strain.

Author response image 1.

ATP levels in the icd mutant. ATP levels of both the mutant and wild-type strains were measured at t=3 hours of cell growth and normalized to cell counts. The figure presents the raw data (a), linear plot (b), and logarithmic plot (c) of the same dataset. This data corresponds to the first panel of Figure 3B in the manuscript.

Author response image 2.

Gentamicin tolerance of wild-type and icd mutant strains of E. coli BW25113. Both wild type and mutant strains were treated with gentamicin (50 µg/ml) for 5 hours at the mid-exponential phase. Cells were plated before and after treatment for CFU/ml counts. The dashed line represents the limit of detection. CFU: Colony forming units.

We think that there are two primary reasons why our study cannot contradict the findings of the Lewis group:

Firstly, our study cannot be directly compared to theirs, as they did not comprehensively explore the impact of gene deletions on cell metabolism beyond the measurement of ATP levels at a single time point (Manuse et al., 2021). Our study encompasses various metabolic parameters such as cellular ATP, redox status, proton motive force (PMF), intracellular pH, and drug uptake throughout the exponential and/or early stationary phase. Additionally, we conducted proteomic analysis for five different strains including mutants and wild type. Moreover, we performed pathway enrichment analysis grounded in the statistical background of the entire genome, encompassing various functional pathway classification frameworks such as Gene Ontology annotations, KEGG pathways, and Uniprot keywords. The results of these pathway enrichment analyses are now available in the Supplementary File (see Supplementary Tables 11-17 in the current manuscript). Thus, we believe it is unjust to deem our study contradictory compared to the Lewis group's study, which does not have a comprehensive analysis of the metabolism of the mutant strains they investigated.

Secondly, our study cannot be compared to that specific study (Manuse et al., 2021) due to the utilization of a distinct antibiotic (ciprofloxacin). Cell tolerance is heavily reliant on the mechanism of action of the antibiotic used. Therefore, the reviewer should have focused on studies closely related to aminoglycoside tolerance. Our study is not confusing or contradictory, as Lewis’ group also demonstrated that the tolerance of the icd mutant to gentamicin was significantly reduced while the tolerance of other TCA cycle mutant strains was increased in a different study (Shan et al., 2015). However, they did not delve into the metabolism of these mutant strains, as we did. We now mention this point in our manuscript (see pages 14-15).

Apart from the confusing data, it is not clear what useful information may be obtained from the choice of the experimental system. The authors examine exponentially growing cells of E. coli for tolerance of aminoglycosides. The population at this stage of growth is highly susceptible to aminoglycosides, and only some rare persister cells can survive. However, the authors do not study persisters. A stationary population of E. coli is tolerant of aminoglycosides, and this is clinically relevant, but this is not the subject of the study.

Response: Respectfully, we must express our disagreement with the reviewer's comments. Our experimental system is meticulously organized and logically structured. Mutant strains such as gltA, sucA, and nuoI deletions exhibit increased tolerance to all aminoglycosides tested, with their fractions clearly increasing around the mid-exponential phase between 3-4 hours (refer to Figure 2B in our manuscript). This surge in tolerance is evident at the population level as well (as depicted in Figure 1A in our manuscript, where certain mutant strains demonstrate complete survival to streptomycin, with survival fractions nearing 1). Given the pronounced increase observed around the mid-exponential phase, we primarily characterize the metabolism of these cells during this growth phase.

It's essential to note that any investigation into antibiotic tolerance and/or resistance holds immense significance, regardless of the growth phase under scrutiny, as antibiotic tolerance/resistance poses a substantial healthcare challenge. Additionally, metabolic mutant strains do not necessarily entail severe fitness costs, as evidenced by Figure S2A published by the Lewis group (Manuse et al., 2021), a finding consistent with our study (see Figure 2B in our manuscript). This phenomenon could confer a survival advantage to bacterial cells, as they may acquire metabolic mutations to bolster their tolerance without incurring significant fitness costs. Furthermore, numerous studies suggest that bacterial cells may opt for the evolutionary pathway leading to increased tolerance before acquiring resistance mechanisms (Levin-Reisman et al., 2017; Santi et al., 2021). The presence of metabolic mutations in clinical E. coli pathogens has also been confirmed through the analysis of a large library of 7243 E. coli genomes from NCBI Pathogen Detection by Collin’s group (Lopatkin et al., 2021). Consequently, comprehending the tolerance mechanisms of metabolic mutations holds paramount importance.

References

Levin-Reisman I, Ronin I, Gefen O, Braniss I, Shoresh N, Balaban NQ. 2017. Antibiotic tolerance facilitates the evolution of resistance. Science (1979) 355:826–830. doi:10.1126/science.aaj2191

Lopatkin AJ, Bening SC, Manson AL, Stokes JM, Kohanski MA, Badran AH, Earl AM, Cheney NJ, Yang JH, Collins JJ. 2021. Clinically relevant mutations in core metabolic genes confer antibiotic resistance. Science (1979) 371. doi:10.1126/science.aba0862

Manuse S, Shan Y, Canas-Duarte SJ, Bakshi S, Sun WS, Mori H, Paulsson J, Lewis K. 2021. Bacterial persisters are a stochastically formed subpopulation of low-energy cells. PLoS Biol 19. doi:10.1371/journal.pbio.3001194

Mohiuddin Kabir M, Shimizu K. 2004. Metabolic regulation analysis of icd-gene knockout Escherichia coli based on 2D electrophoresis with MALDI-TOF mass spectrometry and enzyme activity measurements. Appl Microbiol Biotechnol 65:84–96. doi:10.1007/s00253-004-1627-1

Santi I, Manfredi P, Maffei E, Egli A, Jenal U. 2021. Evolution of Antibiotic Tolerance Shapes Resistance Development in Chronic Pseudomonas aeruginosa Infections. doi:10.1128/mBio.03482-20

Shan Y, Lazinski D, Rowe S, Camilli A, Lewis K. 2015. Genetic basis of persister tolerance to aminoglycosides in Escherichia coli. mBio 6. doi:10.1128/mBio.00078-15

Van den Bergh B, Schramke H, Michiels JE, Kimkes TEP, Radzikowski JL, Schimpf J, Vedelaar SR, Burschel S, Dewachter L, Lončar N, Schmidt A, Meijer T, Fauvart M, Friedrich T, Michiels J, Heinemann M. 2022. Mutations in respiratory complex I promote antibiotic persistence through alterations in intracellular acidity and protein synthesis. Nat Commun 13:546. doi:10.1038/s41467-022-28141-x

Reviewer #2 (Public Review):

Summary:

This interesting study challenges a dogma regarding the link between bacterial metabolism decrease and tolerance to aminoglycosides (AG). The authors demonstrate that mutants well-known for being tolerant to AG, such as those of complexes I and II, are not so due to a decrease in the proton motive force (PMF) and thus antibiotic uptake, as previously reported in the literature.

Strengths:

This is a complete study. These results are surprising and are based on various read-outs, such as ATP levels, pH measurement, membrane potential, and the uptake of fluorophore-labeled gentamicin. Utilizing a proteomic approach, the authors show instead that in tolerant mutants, there is a decrease in the levels of proteins associated with ribosomes (targets of AG), causing tolerance.

Response: We sincerely appreciate the reviewer for taking the time to read our manuscript and offer valuable suggestions.

Weaknesses:

The use of a single high concentration of aminoglycoside: my main comment on this study concerns the use of an AG concentration well above the MIC (50 µg/ml or 25 µg/ml for uptake experiments), which is 10 times higher than previously used concentrations (Kohanski, Taber) in study showing a link with PMF. This significant difference may explain the discrepancies in results. Indeed, a high concentration of AG can mask the effects of a metabolic disruption and lead to less specific uptake. However, this concentration highlights a second molecular level of tolerance. Adding experiments using lower concentrations (we propose 5 µg/ml to compare with the literature) would provide a more comprehensive understanding of AG tolerance mechanisms during a decrease in metabolism.

Another suggestion would be to test iron limitation (using an iron chelator as DIP), which has been shown to induce AG tolerance. Can the authors demonstrate if this iron limitation leads to a decrease in ribosomal proteins? This experiment would validate their hypothesis in the case of a positive result. Otherwise, it would help distinguish two types of molecular mechanisms for AG tolerance during a metabolic disruption: (i) PMF and uptake at low concentrations, (ii) ribosomal proteins at high concentrations.

Response: While we acknowledge the intriguing possibility of exploring whether iron limitation results in a reduction of ribosomal proteins, we believe that this topic falls slightly outside the scope of our current study. This area warrants independent investigation since our current research did not specifically focus on iron-limited environments (LB medium is iron-rich, as referenced (Abdul-tehrani et al., 1999; Rodríguez-Rojas et al., 2015)). However, we fully concur with the notion that experimental outcomes may be contingent upon the concentration of aminoglycosides (AG). Hence, we repeated the critical experiments using a lower concentration of gentamicin (5 µg/mL), as suggested by the reviewer. Before delving into a discussion of these results, we wish to emphasize two key points. Firstly, the majority of our metabolic measurements, including ATP levels, redox activities, intracellular pH, and metabolomics, were conducted in mutant and wild-type cells in the absence of drugs. Our objective was to elucidate the impact of genetic perturbations of the TCA cycle on cell metabolism. Secondly, it's important to emphasize that our study does not invalidate the hypothesis that AG uptake is proton motive force (PMF)-dependent. We observed similar drug uptake across the strains tested, which is reasonable considering that their energy metabolism and PMF are not significantly altered compared to the wild type (at least we did not observe a consistent trend in their metabolic levels). Consequently, our study does not necessarily contradict with previous claims (Taber Harry W et al., 1987). We have now clarified this point in the manuscript (see pages 1 and 13).

When we employed a lower gentamicin concentration, we still noted a significant elevation in tolerance among the gltA, sucA, and nuoI mutant strains compared to the wild type. Also, it remained evident that the observed tolerance in the mutant strains cannot be ascribed to differences in drug uptake or impaired PMF, as the levels of drug uptake and the disruption of PMF by gentamicin (at lower concentrations) in the mutant strains were comparable to those of the wild type. Moreover, since our metabolic measurements and proteomics analyses failed to reveal any notable alterations in energy metabolism in these strains, the consistency in drug uptake levels across both mutant and wild-type strains, even at lower concentrations, further bolsters the validity of our findings obtained at higher gentamicin concentrations. The new results have been incorporated into the Supplementary file (see Supplementary Figures S1, S5, S7, and S9) and discussed throughout the manuscript.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Line 120: Luria-Bertani (LB), used Lysogeny Broth.

Line 180: "RSG dye can be reduced by bacterial reductases of PMF" to be reformulated.

Response: The suggested corrections have been incorporated into the manuscript.

References

Abdul-tehrani H, Hudson AJ, Chang Y, Timms AR, Hawkins C, Williams JM, Harrison PM, Guest JR, Andrews SC. 1999. Ferritin Mutants of Escherichia coli Are Iron Deficient and Growth Impaired, and fur Mutants are Iron Deficient, Journal of Bacteriology.

Rodríguez-Rojas A, Makarova O, Müller U, Rolff J. 2015. Cationic Peptides Facilitate Iron-induced Mutagenesis in Bacteria. PLoS Genet 11. doi:10.1371/journal.pgen.1005546

Taber Harry W, Mueller JP, Miller PF, Arrow AS. 1987. Bacterial Uptake of Aminoglycoside Antibiotics. Microbiol Rev 51:439–457. doi:10.1128/mr.51.4.439-457.1987

Author response:

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

eLife assessment

This manuscript presents a solid and generally convincing set of experiments to address the question of whether the lateral parafacial area (pFL) is active in controlling active expiration, which is particularly important in patient populations that rely on active exhalation to maintain breathing (eg, COPD, ALS, muscular dystrophy). This study presents a valuable finding by pharmacologically mapping the core medullary region that contributes to active expiration and addresses the question of where these regions lie anatomically. Results from these experiments will be of value to those interested in the neural control of breathing and other neuroscientists as a framework for how to perform pharmacological mapping experiments in the future.

Thanks for the positive feedback on our study, as well as the assessment of the novelty of our investigation and the advancements to the field that these results will bring in the future.

We have addressed the specific comments and made changes to the manuscript as indicated below.

Public Reviews:

Reviewer #1 (Public Review):

The main focus of the current study is to identify the anatomical core of an expiratory oscillator in the medulla using pharmacological disinhibition. Although expiration is passive in normal eupneic conditions, activation of the parafacial (pFL) region is believed to evoke active expiration in conditions of elevated ventilatory demands. The authors and others in the field have previously attempted to map this region using pharmacological, optogenetic, and chemogenetic approaches, which present their own challenges.

In the present study, the authors take a systematic approach to determine the precise anatomical location within the ventral medulla's rostrocaudal axis where the expiratory oscillator is located. The authors used a bicuculline (a GABA-A receptor antagonist) and fluorobeads solution at 5 distinct anatomical locations to study the effects on neuronal excitability and functional circuitry in the pFL. The effects of bicuculline on different phases of the respiratory cycle were characterized using a multidimensional cycle-by-cycle analysis. This analysis involved measuring the differences in airflow, diaphragm electromyography (EMG), and abdominal EMG signals, as well as using a phase-plane analysis to analyze the combined differences of these respiratory signals. Anatomical immunostaining techniques were also used to complement the functional mapping of the pFL.

Major strengths of this work include a robust study design, complementary neurophysiological and immunohistochemical methods, and the use of a novel phase-plane analysis. The authors construct a comprehensive functional map revealing functional nuances in respiratory responses to bicuculline along the rostrocaudal axis of the parafacial region. They convincingly show that although bicuculline injections at all coordinates of the pFL generated an expiratory response, the most rostral locations in the lateral parafacial region play the strongest role in generating active expiration. These were characterized by a strong impact on the duration and strength of ABD activation and a robust change in tidal volume and minute ventilation. The authors also confirmed histologically that none of the injection sites overlapped grossly with PHOX2B+ neurons, thus confirming the specificity of the injections in the pFL and not the neighboring RTN.

Collectively, these findings advance our understanding of the presumed expiratory oscillator, the pFL, and highlight the functional heterogeneity in the functional response of this anatomical structure.

Thanks for the positive feedback on the results presented in the current manuscript.

Reviewer #2 (Public Review):

Summary:

Pisanski and colleagues map regions of the brainstem that produce the rhythm for active expiratory breathing movements and influence their motor patterns. While the neural origins of inspiration are very well understood, the neural bases for expiration lag considerably. The problem is important and new knowledge pertaining to the neural origins of expiration is welcome.

The authors perturb the parafacial lateral (pFL) respiratory group of the brainstem with microinjection of bicuculline, to elucidate how disinhibition in specific locations of the pFL influences active expiration (and breathing in general) in anesthetized rats. They provide valuable, if not definitive, evidence that the borders of the pFL appear to extend more rostrally than previously appreciated. Prior research suggests that the expiratory pFL exists at the caudal pole of the facial cranial nucleus (VIIc). Here, the authors show that its borders probably extend as much as 1 mm rostral to VIIc. The evidence is convincing albeit with caveats.

Strengths:

The authors achieve their aim in terms of showing that the borders of the expiratory pFL are not well understood at present and that it (the pFL) extends more rostrally. The results support that point. The data are strong enough to cause many respiratory neurobiologists to look at the sites rostral to the VIIc for expiratory rhythmogenic neurons and characterize their properties and mechanisms. At present my view is that most respiratory neurobiologists overlook the regions rostral to VIIc in their studies of expiratory rhythm and pattern.

Weaknesses:

The injection of bicuculline has indiscriminate effects on excitatory and inhibitory neurons, and the parafacial region is populated by excitatory neurons that are expiratory rhythmogenic and GABA and glycinergic neurons whose roles in producing active expiration are contradictory (Flor et al. J Physiol, 2020, DOI: 10.1113/JP280243). It remains unclear how the microinjections of bicuculline differentially affect all three populations. A more selective approach would be able to disinhibit the populations separately. Nevertheless, for the main point at hand, the data do suggest that we should reconsider the borders of the expiratory pFL nucleus and begin to examine its physiology up to 1 mm rostral to VIIc.

The control experiment showed that bicuculline microinjections induced cFos expression in the pFL, which is good, but again we don't know which neurons were disinhibited: glutamatergic, GABAergic, or glycinergic.

Thanks for sharing your excitement on the results of our study, and appreciating the thorough investigation performed with the use of bicuculline, an approach that was originally used in Pagliardini et al, 2011, PMID: 21414911) and then used by many other groups to generate and study active expiration in vivo.

In the current study we used the well known effect of Bicuculline to systematically test the area that is more sensitive to such a pharmacological effect, and hence may be the core for generating active expiration. While the use of GABA receptor antagonists may have an indiscriminate effect on GABA receptor expressing neurons with various phenotypes, anatomical assessment of inhibitory cells has shown very little distribution of GABAergic and glycinergic cells in the parafacial area (Tanaka et.al, 2003; PMID: 14512139) and it has been inferred in multiple publications (Huckstepp et al., 2015, PMID: 25609622; Huckstepp et al. 2016 PMID: 27300271; Huckstepp et al., 2018, PMID: 30096151; Flor et al., 2020, PMID: 32621515; Britto & Moraes, 2017; PMID: 28004411; Silva et al. 2016; PMID: 26900003) and demonstrated recently (Magalhaes et al.,  2021; PMID: 34510468) that late-E neurons in the parafacial region are excitatory and have a glutamatergic phenotype. We can’t exclude that a small fraction of neurons in the pFL area are inhibitory, and that they could influence recruitment of adjacent late-E expiratory neurons. A more selective activation of neuronal populations with different phenotype would be indeed interesting, nonetheless, if local inhibitory neurons have a role in the generation of active expiration, then their disinhibition could have either an inhibitory effect on late-E activity or stimulate expiration in a more indirect fashion.

While the effect of bicuculline on active expiration has been reported and replicated in multiple manuscripts, the source of inhibition across different phases of the respiratory cycle is still under investigation. Some studies suggest that GABAergic and glycinergic inhibition is not originated in pFL but rather in the BötC and preBötC areas (Flor et al., 2020, PMID: 32621515; Magalhaes et al., 2021; PMID: 34510468) and the effects of this inhibition across the respiratory cycle is debated. Future studies will be key to identify the source of pFL inhibition.

The manuscript characterizes how bicuculline microinjections affect breathing parameters such as tidal volume, frequency, ventilation, inspiratory and expiratory time, as well as oxygen consumption. Those aspects of the manuscript are a bit tedious and sometimes overanalyzed. Plus, there was no predictive framework established at the outset for how one should expect disinhibition to affect breathing parameters. In other words, if the authors are seeking to map the pFL borders, then why analyze the breathing patterns so much? Does doing so provide more insight into the borders of pFL? I did not think it was compellingly argued.

We have edited the introduction to address this comment and emphasize the rationale for the study. We also edited the results section to summarize our findings.

We continue to report our in-depth analysis of the perturbations induced by bicuculline injection over the various respiratory characteristics as this will be fundamental to determine the effects of our experiment not only on the activation of pFL and active expiration, but also on the respiratory network in general. In order to be fair and open about our findings we have reported the results of our analysis in detail. Of note, all sites generated active expiration, but since the objective of the study was to determine the sites with the most significant changes, a finer and multilevel analysis has been used.

Further, lines 382-386 make a point about decreasing inspiratory time even though the data do not meet the statistical threshold. In lines 386-395, the reporting appears to reach significance (line 388) but not reach significance (line 389). I had trouble making sense of that disparity.

The statistics were confirmed, and the lines edited as follows: “Interestingly, the duration of inspiration during the response was found to decrease in all groups relative to baseline respiration (Ti response = 0.279 ± 0.034s, Ti baseline = 0.318 ± 0.043s, Wilcoxon rank sum: Z = 3.24, p = 0.001). Contrary to this decrease in inspiratory duration, the total expiratory time was observed to increase in all groups and remained elevated compared to baseline (TE response = 1.313 ± 0.188s, TE baseline = 1.029 ± 0.161s, Wilcoxon rank sum: Z = 4.49, p = 0.001).”

The other statistical hiccups include "tended towards significance" (line 454), "were found to only reach significance for a short portion of the response" (line 486-7), "did not reach the level of significance" (line 506), which gives one the sense of cherry picking or over-analysis. Frankly, this reviewer finds the paper much more compelling when just asking whether the microinjections evoke active expiration. If yes, then the site is probably part of the pFL.

Statistical “tendencies” have been eliminated throughout the manuscript.

We have analyzed in details our results in order to determine changes and differential effects on respiration when comparing the 5 sites of injections. Although the presentation of the results may seem tedious, it has allowed us to highlight some interesting effects: first, the effects on respiratory frequency. It has been shown in the past that optogenetic stimulation of this area causes an increase in respiratory frequency (Pagliardini et al., 2011, PMID: 21414911), whereas a dishinibition with this same approach or stimulation of AMPAreceptor in pFL have shown a reduction in frequency or not a significant change in the response (Pagliardini et al., 2011, PMID: 21414911; Huckstepp et al., 2015, PMID: 25609622; Huckstepp et al. 2016 PMID: 27300271; Huckstepp et al., 2018, PMID: 30096151). Here, we suggest that the reduction in respiratory frequency is observed only in the caudal sites and could be attributed to BötC effects rather than the stimulation of the core of the pFL since no respiratory change was observe where the effect was more potent (rostral side). Another interesting point was the effects on O2 consumption, although difficult to interpret at this point, we found very interesting that hyperventilation occurred only at the most rostral injection sites.

I encourage the authors to consider the fickleness of p-values in general and urge them to consider not just p but also effect size.

Thank you for the feedback on our description of the statistical results and the suggestion of incorporating effect size. We have now included measurements of effect size in the results section.  Specifically, we calculated the effect size within each ANOVA using the value of eta squared for all data shown in Figures 3 and 4. Please note that in our phase-plane analysis (Fig. 5-6) the Mahalanobis distance is itself an effect size measure for multidimensional data. We also note that statistical evaluation using non-parametric analyses do not involve effect sizes.

Reviewer #3 (Public Review):

Summary:

The study conducted by Pisanski et al investigates the role of the lateral parafacial area (pFL) in controlling active expiration. Stereotactic injections of bicuculline were utilized to map various pFL sites and their impact on respiration. The results indicate that injections at more rostral pFL locations induce the most robust changes in tidal volume, minute ventilation, and combined respiratory responses. The study indicates that the rostrocaudal organization of the pFL and its influence on breathing is not simple and uniform.

Strengths:

The data provide novel insights into the importance of rostral locations in controlling active expiration. The authors use innovative analytic methods to characterize the respiratory effects of bicuculline injections into various areas of the pFL.

Weaknesses:

Bicuculline injections increase the excitability of neurons. Aside from blocking GABA receptors, bicuculline also inhibits calcium-activated potassium currents and potentiates NMDA current, thus insights into the role of GABAergic inhibition are limited.

Increasing the excitability of neurons provides little insights into the activity pattern and function of the activated neurons. Without recording from the activated neurons, it is impossible to know whether an effect on active expiration or any other respiratory phase is caused by bicuculline acting on rhythmogenic neurons or tonic neurons that modulate respiration. While this approach is inappropriate to study the functional extent of the conditional "oscillator" for active expiration, it provides valuable insights into this region's complex role in controlling breathing.

We have included a reflection of the weaknesses of our studies in the technical consideration section to address the possibility that bicuculline may induce active expiration through other mechanisms. Please note that the use of bicuculline was not to gain further insight on GABAergic inhibition of pFL but to adopt a tool to generate active expiration that has been extensively validated by our group and others.

Multiple studies have shown recruitment of excitatory late expiratory neurons with bicuculline injections. Although we did not record from late-E neurons in this study, we infer from the body of literature that disinhibition of neurons in this area will activate late-E neurons (as previously demonstrated) and generate active expiration. Although we see value in recording activity of single neurons (especially to study mechanisms of rhythmogenesis), we opted to measure the physiological response from respiratory muscles as an indication of active expiration recruitment in vivo. Recording from single neurons after bicuculline injections in each site would confirm the presence of expiratory neurons along the parafacial area, which is probably not surprising, since every site tested promoted active expiration. The focus of the study though was to determine the site with the strongest physiological response to disinhibition. Future studies will be key to determine whether all neurons along this column have similar electrophysiological rhythmic properties to the ones recently reported (Magalhaes et al., 2021; PMID: 34510468), or some of them simply provide tonic drive to late-E neurons located elsewhere.

We have discussed the issue as follows:

“Our experiments focused on determining the area in the pFL that is most effective in generating active expiration as measured by ABD EMG activity and expiratory flow. We did not attempt to record single cell neuronal activity at various locations as previously shown in other studies (Pagliardini et al 2011; Magalhaes et al., 2021), as this approach would most likely find some late-E neurons across the pFL and thus not effectively discriminate between areas of the pFL. Future studies involving multi-unit recordings or imaging of cell population activities will help to determine the firing pattern and population density of bicuculline-activated cells and further determine differences in distribution and function of late-E neurons across the region of the pFL.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Overall, the manuscript addresses an important question in the field, the anatomical location of the expiratory oscillator. I commend the authors for a well-thought-out and clearly presented study. However, a few small concerns deserve attention to improve the clarity of the report.

(1) The figures would benefit from a rostral-to-caudal representation of results instead of a caudal-to-rostral orientation. Example, Figure 2.

We opted for a caudal to rostral representation to progressively move away from the inspiratory oscillator (preBötC) and the anatomical reference point (the caudal tip of the facial nucleus) with our series of injections. 

(2) A discussion about how expiratory responses generated by these pharmacological approaches would compare to endogenous baseline conditions. The authors mention that bicuculline injections elicited a late-E downward inflection that was absent in baseline conditions. Thus, this raises the point of how these findings compare to awake freely moving animals or during different conditions of increased ventilatory demand.

This is an interesting question that has not yet been address in the field. As far as we know, there are no recordings of pFL neurons in freely behaving animals although recordings of pFL late-E neurons under elevated PaCO2 have shown a late-E activity in in situ preparations (Britto & Moraes, 2017; PMID: 28004411; Magalhaes et al., 2021; PMID: 34510468).

We have clarified this in the discussion as follows:

“At rest, respiratory activity does not present with active expiration (i.e, expiratory flow below its functional residual capacity in conjunction with expiratory-related ABD muscle recruitment) and expiratory flow occurs due to passive recoil of chest wall with no contribution of abdominal activity. Active expiration and abdominal recruitment can be spontaneously observed during sleep (in particular REM sleep, Andrews and Pagliardini, 2015; Pisanski et al., 2019) and can be triggered during increased respiratory drive (e.g. Hypercapnia, RTN stimulation, Abbott et al., 2011). Although never assessed in freely moving, unanesthetized rodents, bicuculline has been extensively used to generate active expiration and late-E neuron activity in both juvenile and adult anesthetized rats (Pagliardini et al., 2011; Huckstepp et al., 2015 Huckstepp et al., 2016; Huckstepp et al., 2018; De Britto and Moraes, 2017; Magalhaes et al., 2021). “

(3) In Figure 2A, there appears to be an injection site in the top right quadrant of the image, very distant from the intended site. Could the authors confirm if this is an artifact?

Yes, it is an artifact of image acquisition, we should have marked that in the figure. To avoid confusion and follow other reviewers’ suggestions we have edited he figure.

(4) A stylistic suggestion would be to include the subpanel of Figure 2C saline control injection as a graph of its own and also include the control anatomical location in 2B.

Thanks for the suggestion. Because of the complex organization of the figure we opted to leave it as a subpanel in order to not distract the reader from the 5 injection sites, but still provide information about vehicle injection and their lack of changes in respiratory response.

(5) The authors note that DIAm Area (norm.) during the inspiratory phase is increased in the +6 and +8mm groups. However, Figure 5E shows that the +8mm group is significantly reduced as compared to the +6mm group. Please clarify.

During the inspiratory phase we did not observe any significant change in the DIA Area (norm.). We realize that the description of this part of the results was confusing and therefore we have eliminated that section.

Reviewer #2 (Recommendations For The Authors):

I encourage the authors to consider the fickleness of p-values in general and urge them to consider not just p but also effect size. There is a valuable editorial in this week's J Physiology (https://doi.org/10.1113/JP285575) that may provide helpful guidance.

Thanks for this comments and the general assessment. We realized that the results section was dense and with a lot of information. We significantly slimmed the description of the results in order to facilitate the appreciation of the results and avoid confounding statement about significant vs non- significant results.

We have now included measurements of effect size in the results section.  Specifically, we calculated the effect size within each ANOVA using the value of eta squared for all data shown in Figures 3 and 4. Please note that in our phase-plane analysis (Fig. 5-6) the Mahalanobis distance is itself an effect size measure for multidimensional data. We also note that statistical evaluation using non-parametric analyses do not involve effect sizes.

The equipment and resources should be clearly identified and use RRIDs whenever possible. Resources like antibodies and other reagents (e.g., cryoprotectants) should be identified, not just by manufacturer, but also by specific part or product numbers or identifiers.

Manuscript has been edited to add these details.

The manuscript makes reference to ImageJ and Matlab routines, which must be public through GitHub or another stable repository.

Thanks for pointing this out. Image J analysis has been performed following scripts already available to users (no custom scripts). The Matlab scripts used for the multivariate analysis is now available at: https://github.com/mprosteb/Pisanski2024

The way that ABD-DIA coupling was assessed was unclear from the Methods.

The following text has been added to the methods: “The coupling between ABD and DIA signals was measured as a ratio and analyzed by quantifying the number of bursts of activity observed for the ABD and DIA EMG signals during the first 10 minutes of the response, excluding time bins at end of the response (due to fading and waning of the ABD response in those instances).”

Fig. 1A was never cited in the text.

It has been cited now.

Fig. 1A-C appears to be exactly the same as Fig. 5A-C.

The reviewer is correct. We have used figure 1 to describe and explain our analytical methods with sample data and Figure 5 describes our results. We have clarified that in: “Figure 5: Rostral injections elicit more prominent changes to respiration in each signal and sub-period. A-C: Is the same as Method Figure 1, has been included here for further clarity when analyzing the results.”

Late Expiratory airflow is given in units of volts (V) in lines 358-363 (Fig. 4C) but then in units of volts-seconds (V•s) in lines 363-367. Both units are problematic because the voltage is neither an air volume nor an air volume per unit time. Is there some conversion factor left out?

In this section of the results we describe the changes in expiratory peak amplitude (V) and expiratory peak flow (V•s). Since calibration of airflow was performed on the positive flow and for larger volumes, we prefer to use the original units to guarantee precise assessment of the change and avoid introducing potential errors. Since the analysis considers changes from baseline readings, converting to ml or ml*s would not affect our analysis.

Reviewer #3 (Recommendations For The Authors):

The study conducted by Pisanski et al investigates the role of the lateral parafacial area (pFL) in respiratory control, specifically in modulating active expiration. The precise location of this expiratory oscillator within the ventral medulla remains uncertain, with some studies indicating that the caudal tip of the facial nucleus (VIIc) forms the core while others propose more rostral areas. Bicuculline injections were utilized at various pFL sites to explore the impact of these injections on respiration. The authors use innovative and impressive analytic methods to characterize the effect on respiratory activity. The results indicate that injections at more rostral pFL locations induce the most robust changes in tidal volume, minute ventilation, and combined respiratory responses. The study will contribute to an enhanced understanding of the neural mechanisms controlling active expiration. The main message of the study is that the rostro-caudal organization of the pFL is not simple and uniform. The data provides novel insights into the importance of rostral locations in controlling active expiration (see e.g. lines 738-740).

The data and results of the paper are intriguing, and it appears that the experiments are well-managed and executed. However, there are several major and minor comments and suggestions that should be addressed by the authors:

(1) The study relies heavily on local injections into specific areas that are confirmed histologically. One potential concern is the injection volume of 200 nL in such a tiny area. The authors suggest that the drug did not spread to rostral/caudal areas outside the specified coordinate partly based on their cFOS staining. For example, the lack of cFOS activation in TH+ cells and Phox2B cells is interpreted as proof that bicuculline did not spread to these somas (Figure 2). The authors seem to use a similar argument as evidence that the pFL does not include Phox2B neurons in the RTN as discussed in the Discussion section (lines 830-847). However, it is very surprising that bicuculline injections into an area that is known to contain Phox2B and Th+ neurons do not activate these neurons as assessed by the cFOS staining. It seems puzzling to me that none of their injections shown in Figure 2 activated Phox2B or Th neurons. I assume that in targeting the pFL the authors must have sometimes hit areas that included neurons that define the RTN, which would have activated Phox2B or Th+ neurons. Did the authors find that these activations did not activate active expiration? Such negative "controls" would strengthen their argument that pFL is a separate and distinct region that selectively controls active expiration.

Thanks for the positive feedback on the manuscript. As it has been demonstrated and discussed in several previous publications, PHOX2B expressing neurons in this area of the brain are part of the RTN Neuromedin B positive neurons (more densely located in the ventral paraFacial rather than the lateral parafacial, our site of injection), the TH+ C1 neurons (located in a somewhat more caudal and medial position compared to our sites of injection, around the BötC/ preBötC area) and the large Facial MN (easily identifiable by their large size and compact location). Given this differential spatial distribution, and the controls described below, we believe we have reduced the possibility of the direct activation of these neurons, although we can’t exclude it in full.

There is now strong evidence about lack of PHOX2B expression in late E neuron in juvenile and adult rats (Magalhaes et al., 2021; PMID: 34510468). We realize that the microinjected solution could potentially diffuse in the brain and hit other areas, but we combined two strategies to verify our intention for a focal injection activating only a restricted area of the brain (i.e., the pFL): i) localization of fluorobeads that were diluted in the Bicuculline solution; ii) expression of cFos combined with anatomical markers, to identify activated cells. Fluorobeads have a very limited spread in the brain and therefore informed us of the site of the injection to differentiate between the five injections locations. Although we can’t assume that Bicuculline will have a similar spread (and it will also be quickly degraded in the tissue), the combination of this analysis with the localized expression of cFos cells has helped us to differentiate between injections site. Because of the proximity of PHOX2B cells in RTN and C1 neurons, we also combined cFos expression with immunohistochemistry to determine whether bicuculline activation was also visible in these two neuronal populations. Our results indicate that there is baseline cfos activity in RTN neurons (see vehicle injection) but the fraction of PHOX2B activated cells did not increase with bicuculline injections suggesting that these neurons were not the target of our injections. Please note that cfos expression has been extensively used to determine RTN neuron activation, especially following chemoreflex responses. 

(2) The authors refer to "the expiratory oscillator" throughout the manuscript (e.g. lines 58, 62, 65) as if there is only one expiratory oscillator i.e. "the expiratory oscillator". For some reason, the authors avoided citing and mentioning PiCo (Anderson et al. 2016), which is considered the oscillator for postinspiration. Since the present study focuses on the role of expiration, and since the authors describe convincing effects on postinspiration, considering this oscillator which is located dorsomedial to the VRC seems relevant for the present study.

Due to the limited and controversial literature that is currently present describing Pico as a third oscillator and the fact that our studies do not directly assess the post-inspiratory activity (as measure by the V nerve or laryngeal muscles) or Pico activity and location (which would be even more distant than the RTN, for example), we prefer to avoid commenting on the effects of this injection on Pico or the connectivity between Pico and pFL.

We have added this to the discussion:

“Therefore, although it has previously been described, it is currently unknown the exact mechanism by which this post-I activity in the ABD muscles is generated. For example the interplay between the rostral pFL and brainstem structures generating post-inspiratory activity, such as the proposed post-inspiratory oscillator (PiCo; Anderson et al., 2016) or pontine respiratory networks, could be reasonably involved in this process.”

(3) The authors do not specify what type of bicuculline they injected. Bicuculline is known to have significant effects on potassium channels. Thus, the effects reported here could be due to a non-specific change in excitability, rather than caused by a specific GABAergic blockade.

The authors also do not know what effects these injections cause in the neurons in vivo, since the injections are not accompanied by recordings from the respiratory neurons that they activate. This together with the non-specific bicuculline effects will affect the interpretation of the results. Thus, the authors need to be more careful when interpreting their effects as "GABAergic". The use of more specific blockers like gabazine could partly address this concern. The authors have to discuss this in a "limitation section".

Thanks for pointing that out, we have now clarified in the methods section that we used bicuculline methochloride. We can’t exclude that some side- effects could be present due to the use of this drug. For the purpose of this study though, we focused on using bicuculline as a tool to consistently generate active expiration since it has been extensively used by multiple laboratories to induce abdominal muscle recruitment and active expiration, as well as to directly record late-E neurons in this same area.

We have included in the discussion the following statement:

“Technical considerations

Bicuculline methiodide has previously been observed to exhibit inhibitory effects on Ca2+ activated K+ currents inducing non-specific potentiation of NMDA currents (Johnson and Seutin, 1997). Consequently, caution is warranted in attributing our findings solely to the GABAa antagonist properties of bicuculline. Previous work has demonstrated a temporal correlation between the onset of late-E neuron activity in the caudal parafacial region and ABD activity in response to bicuculline (Pagliardini et al., 2011; de Britto and Moraes, 2017; Magalhaes et al., 2021) as well as GABAergic sIPSCs in late-E neurons (Magalhaes et al., 2012). However, it is essential to note that the current study lacks single unit recording, preventing us from definitively confirming whether the observed activity stems from late-E neuronal GABAergic dishinibition or excitation through non GABAergic mechanisms.”

(4) I also caution the authors when stating that the bicuculline injections will reveal the precise location and functional boundaries of "the" expiratory oscillation within the pFL. Increasing the excitability with bicuculline is inappropriate to study the functional boundaries of an oscillator. It is particularly inappropriate to identify the boundaries of the pFL, a network that is normally inactive and activated only under certain behavioral and metabolic conditions. Because the injections are increasing the neuronal excitability unspecifically, and because the authors are not recording the activity of the neurons in the pFL region it is unclear what kind of neurons are activated. The cFOS staining may help to define whether these neurons are Phox2B or Th positive or negative, but they will not provide insights into the activity patterns of the activated neurons. Thus, it is fair to assume that these injections will likely include also tonic neurons that might indirectly control the activity of pFL neurons under certain metabolic or behavioral conditions without actually being involved in the rhythmogenesis of active expiration. Many of the effects peak after several minutes, and different regions cause differential effects with different time courses, which is difficult to interpret functionally. Thus, the "core" identified in the present study could consist of tonic neurons as opposed to rhythmic neurons generating active expiration.

We agree with the reviewer that our local injections may have activated an heterogeneous population of neurons. We do not claim that we only activated late-E rhythmogenic neurons but that our multiple sites of injections revealed the area that is generating the strongest excitation of ABD muscles and active expiration.

While the use of GABA receptor antagonists may have an indiscriminate effect on GABA receptor expressing neurons with various phenotypes, anatomical assessment of inhibitory cells has shown very little distribution of GABAergic and glycinergic cells in the parafacial area (Tanaka et.al, 2003; PMID: 14512139) and it has been inferred in multiple publications (Huckstepp et al., 2015, PMID: 25609622; Huckstepp et al. 2016 PMID: 27300271; Huckstepp et al., 2018, PMID: 30096151; Flor et al., 2020, PMID: 32621515; Britto & Moraes, 2017; PMID: 28004411; Silva et al. 2016; PMID: 26900003) and demonstrated recently (Magalhaes et al.,  2021; PMID: 34510468) that late-E neurons in the parafacial region are excitatory and have a glutamatergic phenotype

As suggested by the reviewer, it is possible that the bicuculline injection may have activated some tonic non rhythmogenic neurons which could activate the expiratory oscillator located elsewhere.

We have edited the introduction as follows:

“By strategically administering localized volumes of bicuculline at multiple rostrocaudal levels of the ventral brainstem, we aimed to selectively enhance the excitability of neurons driving active expiration, thereby revealing the extension of the pharmacological response and the most efficient site in generating active expiration.”

We have edited the results as follows:

“Importantly, the group with injection sites at +0.6 mm from VIIc exhibited the swiftest response onset, suggesting that this area is the most critical for the generation of active expiration, either through direct activation of the expiratory oscillator or, alternatively, for providing a strong tonic drive to late-E neurons located elsewhere.”

In the introduction, it should also be emphasized that the pharmacological approach used in the present study complements the existing elegant chemogenetic studies, rather than emphasizing primarily the limitations of the chemogenetic inhibitions. The conclusion should be that these studies together provide different, yet complementary insights: The chemogenetic approach by inhibiting neurons, the present study by exciting neurons, and all studies come with their own limitations.

Thanks for the suggestion, we have updated the manuscript as follows:

“Although both of these elegant chemogenetic studies have contributed extensively to our understanding of the pFL, the existing evidence suggests that the expiratory oscillator may expand beyond the limits of the viral expression achieved in said studies, as proposed by Huckstepp et al., (2015).”

Throughout the manuscript, the authors have to be cautious when implying that an excitatory effect relates to the activity of rhythmogenic pFL neurons. For example, on line 710 the authors state that "it is conceivable to infer that the rostral pFL is in the closest proximity to the cells responsible for the generation of active expiration". While it may indeed be "conceivable", the bicuculline injections themselves provide no insights into the location of neurons responsible for rhythmogenesis. It is equally "conceivable" that the excited neurons provide a tonic drive to the neurons without being involved in the generation of active expiration. These tonic neurons could be located at a distance from the presumed rhythmogenic core.

We have included the possibility of tonic excitation in the technical considerations section:

“However, our study did not include recording from late-E neurons following bicuculline injections, preventing us from definitively confirming whether the observed activity stems from late-E neuronal excitation or the potentiation of a tonic drive, particularly in the rostral areas.”

(5) It is intriguing that some of their injections (Fig.2D) evoked postinspiratory activity. This interesting finding should be discussed as it could provide important insights into the coordination of the different phases of expiration.

Thanks for the suggestion. We have included the following to the discussion:

“Therefore, although it has previously been described, the exact mechanism by which this post-I ABD activity is generated is unclear. This late-E/post-I pattern of activity is similar to what has been observed in in vitro preparations and in vivo recordings in juvenile rats (Janczewski et al., 2002; Janczewski et al., 2006).

“Therefore, although it has previously been described, it is currently unknown the exact mechanism by which this post-I activity in the ABD muscles is generated. For example the interplay between the rostral pFL and brainstem structures generating post-inspiratory activity, such as the proposed post-inspiratory oscillator (PiCo; Anderson et al., 2016) or pontine respiratory networks, could be reasonably involved in this process.”

(6) The authors conducted bilateral disinhibition of the pFL, but only a unilateral photomicrograph was shown. Figure 2 should include a representative bilateral photomicrograph along with a scatter plot for clarity and completeness.

We have edited figure 2 to include representative images of bilateral injections.

(7) Regarding the Bicuculline injections in the Methods section: Aside from specifying exactly what type of bicuculline was used, the authors should provide more information about the pFL location and landmarks used, including the missing medial-lateral coordinate. The fluorobead spread of approximately ~300 µm, as observed in Figure 2C, is crucial for the interpretation of the results and should be detailed. An alternative approach could involve e.g. calculating the area covered by fluorobeads in each group.

We have included the following in the text:

“Each rat was injected at 2.8 mm lateral from the midline and at a specific RC coordinate based on the following groups: -0.2 mm from the caudal tip of the facial nucleus (VIIc) (n=5), +0.1 mm from VIIc (n=7), +0.4 mm from VIIc (n=5), +0.6 mm from VIIc (n=6), +0.8 mm from VIIc (n=5)”

“These findings strongly suggest that bicuculline specifically activated cells within the vicinity of the injection sites which spread ~300 ìm (Figure 2C, horizontal lines) and did not activate PHOX2B+ cells in the RTN area, beyond their baseline level of activity.”

(8) In the Experimental Protocol, the authors should provide more details on how the parameters were determined. For example, specify the number of cycles included for Dia frequency/amplitude, Abd frequency/amplitude, and with regards to the averaging process, the authors should specify over how many cycles they obtained an average for Dia/Abd activity time and AUC. The authors should also provide information on the number of bicuculline injections that they repeated to average these values and they should report the coefficient of variation for repeated injections. Please clarify the method used to calculate AUC, considering the non-linear nature of the activity.

Only one bicuculline injection per rat was performed and the number of rats used for each injection site is indicated in the methods as follows:

“Each rat was injected at 2.8 mm lateral from the midline and at a specific RC coordinate based on the following groups: -0.2 mm from the caudal tip of the facial nucleus (VIIc) (n=5), +0.1 mm from VIIc (n=7), +0.4 mm from VIIc (n=5), +0.6 mm from VIIc (n=6), +0.8 mm from VIIc (n=5), and CTRL (n=7). We recorded the physiological responses to the injection for 20-25 min.”

We have clarified in the methods section the following:

“Respiratory data was tracked in time bins of 2-minute duration from the baseline period prior to injections and spanned 20 min of recording post-injection. Mean-cycle measurements for each signal were computed by averaging values across all cycles within a given time bin.”

Additional clarifications have been added:

“We then used the average calculations of respiratory rate (RR), tidal volume (VT), Minute Ventilation (Ve), expiratory ABD amplitude, expiratory ABD area, VO2, VE/VO2 to obtain values relative to the baseline period. Peak responses were identified as the time bin that produced the strongest changes relative to baseline.”

“Mean-cycle measurements for each signal were computed by averaging across all cycles within a given time bin. (~300 cycles in baseline, ~100 cycles per response time bin). We then used the average calculations of respiratory rate (RR), tidal volume (VT), Minute Ventilation (Ve), expiratory ABD amplitude, expiratory ABD area, VO2, VE/VO2 to obtain values relative to the baseline period. Peak responses were identified as the time bin that produced the strongest changes relative to baseline.”

“The Area under the curve (AUC) was measured during baseline and was subtracted from the corresponding AUC of the response for each time bin (Figure 1C). This AUC measure was computed as the sum of the signal in a given respiratory phase as all signals were sampled at the same rate. Note that areas calculated below the zero- (0) line, as would be expected from a negative airflow during expiration, yields negative AUC values.”

(9) The authors should explain how oxygen consumption was calculated-did it involve the Depocas & Hart (1957) formula? Please provide information on expiratory CO2, whether ventilation was adjusted to achieve consistent CO2 levels across animals, and ideally specify the end-tidal CO2 range for the experiments. Discuss the rationale behind the chosen CO2 levels and whether CO2-dependent pFL activity could have influenced results.

We have clarified in the measurement in the methods as follows:

“The gas analyzer measured fractional concentration of O2. Based on this and the flow rate at the level of the trachea (minute ventilation), we calculated O2 consumption according to Depocas and Hart (1957).”

We have also added to the methods section:

“During the entire experimental procedure, rats breathed spontaneously and end tidal CO2 was not adjusted through the experimental protocol.”

In terms of the CO2-dependent pFL activity possibly influencing the results: by inducing active expiration in conditions in which there is no physiological demand for it (i.e. no hypoxia or hypercapnia), it is likely that pCO2 is reduced, overall decreasing the drive for ABD activity which would suggest that our results are likely an underestimation of the response that would have been produced if we maintained the CO2 levels constant.

(10) The authors should address the discrepancy in fos-activated neurons between the control (44 neurons) and experimental animals (90-120 neurons per hemisection). Please explain the activation in the control group. Please also provide insights into how the authors interpret this difference in cfos-activated neurons between control and experimental groups.

The following paragraph has been added to the discussion:

“The assessment of cellular activity, quantified through cFos staining, unveiled the existence of basal activity in control rats. This observed baseline activity is likely emanating from subthreshold physiological processes within the parafacial area which do not culminate in ABD activity. Analysis of the cFos staining confirmed focal activation of neurons in the pFL of rats injected with bicuculline and minimal cFos expression in the PHOX2B+ cells in all groups as compared to the control group. These results confirm the very limited mediolateral spread of the drug from the core site of injection and back previous findings supporting the hypothesis that the majority of PHOX2B+ cells are more ventrally located in the parafacial area (pFV, Huckstepp et al., 2015) and PHOX2B+ cell recruitment is not necessary for active expiration (de Britto & Moraes, 2017; Magalhães et al., 2021).”

(11) In Figure 8, the authors plotted the relationship of each cycle correlated to the normalized area. Have you also calculated the same late-E, inspiratory, and post-I to fR or VT separately?

No, we only did the separated breathing phase (late-E, I, Post-I) analysis in the calculations of the DIA, airflow and ABD area, as well as on the Euclidean and Mahalanobis distances.

Minor comments:

Is there any specific reason for conducting these experiments exclusively in males?

No, we usually use male rats for this type of experiments. We use both male and female rats for other studies that concern the effects of sex hormones but in this case, we performed experiments only in male rats.

Page 13, Line 320: What is the duration of the bicuculline-induced effects?

This information is included in the results section as follows:

“Similarly, the ABD response duration was longer at the two most rostral locations (+0.6 mm = 17.6 ± 2.7 min; +0.8 = 17.1 ± 3.3 min) compared to the most caudal group (-0.2 mm = 2.4 ± 1.1 min; One-Way ANOVA p = 0.043; Tukey -0.2 mm vs +0.6 mm: p = 0.048; -0.2 mm vs +0.8 mm: p = 0.041; Figure 3E).”

Page 16, Line 400: Is there a rationale for the high tidal volume (VT) observed in these animals? A baseline VT of 7 ml/kg appears notably elevated.

Please note that rats were vagotomised and spontaneously breathing, hence the tidal volume is increased compared to non-vagotomised rats as seen in previous studies (Ouahchi et al., 2011).

Figure 2D: Could you provide longer recordings? Additionally, incorporating diaphragm (Dia) recordings would enhance the interpretation of abdominal (Abd) recordings.

Figure 3 A has a representative example of the 20 minute recordings for each location.

Page 18, Line 458: Please rectify "Dunn: p , 0.001" to the appropriate format, perhaps "Dunn: p < 0.001."

Thank you, edited.

Author response:

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

eLife assessment

This fundamental study investigates the transcriptional changes in neurons that underlie loss of learning and memory with age in C. elegans, and how cognition is maintained in insulin/IGF-1-like signaling mutants. The presented evidence is compelling, utilizing a cutting-edge method to isolate neurons from worms for genomics that is clearly conveyed with a rigorous experimental approach. Overall, this study supports that older daf-2 worms maintain cognitive function via mechanisms that are unique from younger wild type worms, which will be of great interest to neuroscientists and researchers studying ageing.

Public Reviews:

Reviewer #1 (Public Review):

The authors perform RNA-seq on FACS isolated neurons from adult worms at days 1 and 8 of adulthood to profile the gene expression changes that occur with cognitive decline. Supporting data are included indicating that by day 7 of adulthood, learning and memory are reduced, indicating that this timepoint or after represents cognitively aged worms. Neuronal identity genes are reduced in expression within the cognitively aged worms, whereas genes involved in proteostasis, transcription/chromatin, and the stress response are elevated. A number of specific examples are provided, representing markers of specific neuronal subtypes, and correlating expression changes to the erosion of particular functions (e.g. motor neurons, chemosensory neurons, aversive learning neurons, etc).

To investigate whether upregulation of genes in neurons with age is compensatory or deleterious, the authors reduced expression of a set of three significantly upregulated genes and performed behavioral assays in young adults. In each case, reduction of expression improved memory, consistent with a model in which age-associated increases impair neuronal function.

The authors then characterize learning and memory in wild type, daf-2, and daf-2/daf-16 worms with age and find that daf-2 worms have an extended ability to learn for approximately 10 days longer that wild types. This was daf-16 dependent. Memory was extended in daf-2 as well, and strikingly, daf-2;daf-16 had no short term memory even at day 1. Transcriptomic analysis of FACS-sorted neurons was performed on the three groups at day 8. The authors focus their analysis on daf-2 vs. daf-2;daf-16 and present evidence that daf-2 neurons express a stress-resistance gene program. They also find small differences between the N2 and daf-2;daf-16 neurons, which correlate with the observed behavioral differences, though these differences are modest.

The authors tested eight candidate genes that were more highly expressed in daf-2 neurons vs. daf-2;daf-16 and showed that reduction of 2 and 5 of these genes impaired learning and memory, respectively, in daf-2 worms. This finding implicates specific neuronal transcriptional targets of IIS in maintaining cognitive ability in daf-2 with age, which, importantly, are distinct from those in young wild type worms.

Overall, this is a strong study with rigorously performed experiments. The authors achieved their aim of identifying transcriptional changes in neurons that underlie loss of learning and memory in C. elegans, and how cognition is maintained in insulin/IGF-1-like signaling mutants. 

We thank you for the evaluation and response.

Reviewer #2 (Public Review):

Weng et al. perform a comprehensive study of gene expression changes in young and old animals, in wild-type and daf-2 insulin receptor mutants, in the whole animal and specifically in the nervous system. Using this data, they identify gene families that are correlated with neuronal ageing, as well as a distinct set of genes that are upregulated in neurons of aged daf-2 mutants. This is particularly interesting as daf-2 mutants show both extended lifespan and healthier neurons in aged animals, reflected by better learning/memory in older animals compared with wild-type controls. Indeed, knockdown of several of these upregulated genes resulted in poorer learning and memory. In addition, the authors showed that several genes upregulated during ageing in wild-type neurons also contribute to learning and memory; specifically, knockdown of these genes in young animals resulted in improved memory. This indicates that (at least in this small number of cases), genes that show increased transcript levels with age in the nervous system somehow suppress memory, potentially by having damaging effects on neuronal health.

Finally, from a resource perspective, the neuronal transcriptome provided here will be very useful for C. elegans researchers as it adds to other existing datasets by providing the transcriptome of older animals (animals at day 8 of adulthood) and demonstrating the benefits of performing tissue-specific RNAseq instead of whole-animal sequencing.

The work presented here is of high quality and the authors present convincing evidence supporting their conclusions. I only have a few comments/suggestions:

(1) Do the genes identified to decrease learning/memory capacity in daf-2 animals (Figure 4d/e) also impact neuronal health? daf-2 mutant worms show delayed onset of age-related changes to neuron structure (Tank et al., 2011, J Neurosci). Does knockdown of the genes shown to affect learning also affect neuron structure during ageing, potentially one mechanism through which they modulate learning/memory? 

(2) The learning and memory assay data presented in this study uses the butanone olfactory learning paradigm, which is well established by the same group. Have the authors tried other learning assays when testing for learning/memory changes after knockdown of candidate genes? Depending on the expression pattern of these genes, they may have more or less of an effect on olfactory learning versus for e.g. gustatory or mechanosensory-based learning.

(3) A comment on the 'compensatory vs dysregulatory' model as stated by the authors on page 7 - I understand that this model presents the two main options, but perhaps this is slightly too simplistic: gene expression that rises during ageing may be detrimental for memory (= dysregulatory), but at the same time may also be beneficial other physiological roles in other tissues (=compensatory). 

Thank you for your original suggestions; we addressed them in the previous version of response to the reviewers.

Comments on revised version:

I am satisfied with how the authors have addressed all my comments/suggestions. 

Thank you for your response!

Reviewer #3 (Public Review):

Summary

In this manuscript, Weng et al. identify the neuron specific transcriptome that impacts age dependent cognitive decline. The authors design a pipeline to profile neurons from wild type and long-lived insulin receptor/IGF-1 mutants using timepoints when memory functions are declining. They discover signatures unique to neurons which validates their approach. The authors identify that genes related to neuronal identity are lost with age in wild type worms. For example, old neurons reduce the expression of genes linked to synaptic function and neuropeptide signaling and increase the expression of chromatin regulators, insulin peptides and glycoproteins. Depletion of selected genes which are upregulated in old neurons (utx-1, ins-19 and nmgp-1) leads to improved short memory function. This indicates that some genes that increase with age have detrimental effects on learning and memory. The pipeline is then used to test neuronal profiles of long-lived insulin/IGF-1 daf-2 mutants. Genes related to stress response pathways are upregulated in long lived daf-2 mutants (e.g. dod-24, F08H9.4) and those genes are required for improved neuron function.

Strengths

The manuscript is well written, and the experiments are well described. The authors take great care to explain their reasoning for performing experiments in a specific way and guide the reader through the interpretation of the results, which makes this manuscript an enjoyable and interesting read. The authors discover novel regulators of learning and memory using neuron-specific transcriptomic analysis in aged animals, which underlines the importance of cell specific deep sequencing. The timepoints of the transcriptomic profiling are elegantly chosen, as they coincide with the loss of memory and can be used to specifically reveal gene expression profiles related to neuron function. The authors discuss on the dod-24 example how powerful this approach is. In daf-2 mutants whole-body dod-24 expression differs from neuron specific profiles, which underlines the importance of precise cell specific approaches. This dataset will provide a very useful resource for the C. elegans and aging community as it complements existing datasets with additional time points and neuron specific deep profiling.

Weakness

This study nicely describes the neuron specific profiles of aged long-lived daf-2 mutants. Selected neuronal genes that were upregulated in daf-2 mutants (e.g. F08H9.4, mtl-1, dod-24, alh-2, C44B7.5) decreased learning/memory when knocked down. However, the knock down of these genes was not specific to neurons. The authors use a neuron-sensitive RNAi strain to address this concern and acknowledge this caveat in the text. While it is likely that selected candidates act only in neurons it is possible that other tissues participate as well.

Thank you for pointing this caveat out. We have mentioned it in the figure legend.

Author response:

Reviewer #1 (Public Review):

Summary:

This computational modeling study builds on multiple previous lines of experimental and theoretical research to investigate how a single neuron can solve a nonlinear pattern classification task. The authors construct a detailed biophysical and morphological model of a single striatal medium spiny neuron, and endow excitatory and inhibitory synapses with dynamic synaptic plasticity mechanisms that are sensitive to (1) the presence or absence of a dopamine reward signal, and (2) spatiotemporal coincidence of synaptic activity in single dendritic branches. The latter coincidence is detected by voltage-dependent NMDA-type glutamate receptors, which can generate a type of dendritic spike referred to as a "plateau potential." The proposed mechanisms result in moderate performance on a nonlinear classification task when specific input features are segregated and clustered onto individual branches, but reduced performance when input features are randomly distributed across branches. Given the high level of complexity of all components of the model, it is not clear which features of which components are most important for its performance. There is also room for improvement in the narrative structure of the manuscript and the organization of concepts and data.

To begin with, we will better explain the goal of the study in the introduction and explain that it relies on earlier theoretical work. The goal of the study was to investigate whether and how detailed neuron models with biologically-based morphologies, membrane properties, ion channels, dendritic nonlinearities, and biologically plausible learning rules can quantitatively account for the theoretical results obtained with more abstract models.

We will further evaluate and clarify the roles of several components in our model regarding their impact on the results. These include a) the role of sufficiently robust and supralinear plateau potentials in computing the NFBP; and b) the importance of metaplasticity for individual synapses, allowing them to start or stop responding to relevant or irrelevant stimuli, respectively, over the training period.

Strengths:

The integrative aspect of this study is its major strength. It is challenging to relate low-level details such as electrical spine compartmentalization, extrasynaptic neurotransmitter concentrations, dendritic nonlinearities, spatial clustering of correlated inputs, and plasticity of excitatory and inhibitory synapses to high-level computations such as nonlinear feature classification. Due to high simulation costs, it is rare to see highly biophysical and morphological models used for learning studies that require repeated stimulus presentations over the course of a training procedure. The study aspires to prove the principle that experimentally-supported biological mechanisms can explain complex learning.

Weaknesses:

The high level of complexity of each component of the model makes it difficult to gain an intuition for which aspects of the model are essential for its performance, or responsible for its poor performance under certain conditions. Stripping down some of the biophysical detail and comparing it to a simpler model may help better understand each component in isolation. That said, the fundamental concepts behind nonlinear feature binding in neurons with compartmentalized dendrites have been explored in previous work, so it is not clear how this study represents a significant conceptual advance. Finally, the presentation of the model, the motivation and justification of each design choice, and the interpretation of each result could be restructured for clarity to be better received by a wider audience.

To achieve the goal of the study as described above, we chose to use a biophysically and morphologically detailed neuron model to see if it could quantitatively account for the theoretically-based nonlinear computations, for instance, those discussed in Tran-Van-Minh, A. et al. (2015).

We will explain the role of each component of the learning rule, as well as the dendritic nonlinearities, for the performance on the NFBP.

Reviewer #2 (Public Review):

Summary:

The study explores how single striatal projection neurons (SPNs) utilize dendritic nonlinearities to solve complex integration tasks. It introduces a calcium-based synaptic learning rule that incorporates local calcium dynamics and dopaminergic signals, along with metaplasticity to ensure stability for synaptic weights. Results show SPNs can solve the nonlinear feature binding problem and enhance computational efficiency through inhibitory plasticity in dendrites, emphasizing the significant computational potential of individual neurons. In summary, the study provides a more biologically plausible solution to single-neuron learning and gives further mechanical insights into complex computations at the single-neuron level.

Strengths:

The paper introduces a novel learning rule for training a single multicompartmental neuron model to perform nonlinear feature binding tasks (NFBP), highlighting two main strengths: the learning rule is local, calcium-based, and requires only sparse reward signals, making it highly biologically plausible, and it applies to detailed neuron models that effectively preserve dendritic nonlinearities, contrasting with many previous studies that use simplified models.

Indeed, the learning rule is local and reward-based, and we will highlight better in the paper that it is “always on”, i.e. there are no separate training and testing phases.

Weaknesses:

I am concerned that the manuscript was submitted too hastily, as evidenced by the quality and logic of the writing and the presentation of the figures. These issues may compromise the integrity of the work. I would recommend a substantial revision of the manuscript to improve the clarity of the writing, incorporate more experiments, and better define the goals of the study.

We will revise the manuscript thoroughly to better present the figures and writing (more detailed below). We will also show supplementary figures showcasing the role of the different components of the learning rule.

Major Points:

(1) Quality of Scientific Writing: The current draft does not meet the expected standards. Key issues include:

i. Mathematical and Implementation Details: The manuscript lacks comprehensive mathematical descriptions and implementation details for the plasticity models (LTP/LTD/Meta) and the SPN model. Given the complexity of the biophysically detailed multicompartment model and the associated learning rules, the inclusion of only nine abstract equations (Eq. 1-9) in the Methods section is insufficient. I was surprised to find no supplementary material providing these crucial details. What parameters were used for the SPN model? What are the mathematical specifics for the extra-synaptic NMDA receptors utilized in this study? For instance, Eq. 3 references [Ca2+]-does this refer to calcium ions influenced by extra-synaptic NMDARs, or does it apply to other standard NMDARs? I also suggest the authors provide pseudocodes for the entire learning process to further clarify the learning rules.

The detailed setup of the model is described in the referenced papers, including equations and parameter values. The model is downloadable on github. For this reason we did not repeat the information here. That said, we will go through the manuscript and clarify all details, and provide supplemental figures and a GitHub link where necessary for reproducing the results.

ii. Figure quality. The authors seem not to carefully typeset the images, resulting in overcrowding and varying font sizes in the figures. Some of the fonts are too small and hard to read. The text in many of the diagrams is confusing. For example, in Panel A of Figure 3, two flattened images are combined, leading to small, distorted font sizes. In Panels C and D of Figure 7, the inconsistent use of terminology such as "kernels" further complicates the clarity of the presentation. I recommend that the authors thoroughly review all figures and accompanying text to ensure they meet the expected standards of clarity and quality.

We will revise the figures for consistency and clarity.

iii. Writing clarity. The manuscript often includes excessive and irrelevant details, particularly in the mathematical discussions. On page 24, within the "Metaplasticity" section, the authors introduce the biological background to support the proposed metaplasticity equation (Eq. 5). However, much of this biological detail is hypothesized rather than experimentally verified. For instance, the claim that "a pause in dopamine triggers a shift towards higher calcium concentrations while a peak in dopamine pushes the LTP kernel in the opposite direction" lacks cited experimental evidence. If evidence exists, it should be clearly referenced; otherwise, these assertions should be presented as theoretical hypotheses. Generally, Eq. 5 and related discussions should be described more concisely, with only a loose connection to dopamine effects until more experimental findings are available.

The reviewer is correct; the cited text does not present experimental facts but rather illustrates how the learning rule operates. We will revise the section on the construction of learning rules to clarify which aspects are explicit assumptions and which are experimentally verified. In particular, we will provide a more detailed description and motivation for metaplasticity

(2) Goals of the Study: The authors need to clearly define the primary objective of their research. Is it to showcase the computational advantages of the local learning rule, or to elucidate biological functions?

Briefly, the goal of the study was to investigate whether earlier theoretical results with more abstract models can be quantitatively recapitulated in morphologically and biophysically detailed neuron models with dendritic nonlinearities and with biologically based learning rules. (similar response to Summary and Weaknesses to Reviewer #1). We will update the introduction with this information.

i. Computational Advantage: If the intent is to demonstrate computational advantages, the current experimental results appear inadequate. The learning rule introduced in this work can only solve for four features, whereas previous research (e.g., Bicknell and Hausser, 2021) has shown capability with over 100 features. It is crucial for the authors to extend their demonstrations to prove that their learning rule can handle more than just three features. Furthermore, the requirement to fine-tune the midpoint of the synapse function indicates that the rule modifies the "activation function" of the synapses, as opposed to merely adjusting synaptic weights. In machine learning, modifying weights directly is typically more efficient than altering activation functions during learning tasks. This might account for why the current learning rule is restricted to a limited number of tasks. The authors should critically evaluate whether the proposed local learning rule, including meta-plasticity, actually offers any computational advantage. This evaluation is essential to understand the practical implications and effectiveness of the proposed learning rule.

As mentioned above, our intent is not to demonstrate the computational advantages of the proposed learning rule but to investigate and illustrate how biophysically detailed neuron models that also display dendritic plateau potential mechanisms, together with biologically-based learning rules, can support the theoretically predicted computational requirements for complex neuronal processing (e.g., Tran-Van-Minh, A. et al., 2015), as well as the results obtained with more abstract neuron models and plateau potential mechanisms (e.g., Schiess et al., 2016; Legenstein and Maass, 2011).

In the revised manuscript, we will also discuss the differences between the supervised learning rule in Bicknell and Hausser (2021) and our local and reward-based learning rule. We will also show a critical evaluation of how our local learning rule and metaplasticity affect the synaptic weights and why the different components of the rule are needed.

ii. Biological Significance: If the goal is to interpret biological functions, the authors should dig deeper into the model behaviors to uncover their biological significance. This exploration should aim to link the observed computational features of the model more directly with biological mechanisms and outcomes.

We will make an attempt to better link the learning rule and dendritic supra-linearities and interpret their biological function.

Author response:

eLife assessment

“…The evidence however is incomplete, since the tai loss-of-clone phenotype is based on one allele and the mechanism involved in cell competition through Dlp and Wg lacks adequate supporting data.”

We agree with the need for a second allele and are adding supporting data from a new tai lof allele we have generated by Crispr.

We also agree that additional functional data would help demonstrate that differences in Dlp levels are required for the mechanism of Tai cell competition. Experiments are ongoing to test whether normalizing Dlp levels across clonal boundaries rescues elimination of Tai-low clones.

Reviewer #1:

Overall Statements:

“There is some data in the supplementary materials suggesting that Tai promotes dlp mRNA expression, but this was not compelling.”

We are currently testing effects on Tai on dlp and dally transcription using qPCR and reporter transgenes. As noted below, the effects of Tai on Dlp trafficking are ‘strong’, so resolving effects on Dlp transcription will complement this localization data.

“The authors don't further examine Dlp protein in tai clones.”

As noted by the Reviewer, we do examine Dlp levels and localization in tai-low clones (see Figure 9), but these experiments are challenging due to their very small size and the hypomorphic nature of the tai allele (tai[k15101]) that was used. Experiments are in progress to examine the effect of our Crispr null allele of tai on Dlp levels and localization in wing clones.

“In sum, the authors have uncovered some interesting results, but the story has some unresolved issues that, if addressed, could boost its impact. Additionally, the preprint seems to have 2 stories, one about tai and cell competition and the other about tai and Wg distribution. It would be helpful to reorder the figures and improve the narrative so that these are better integrated with each other.”

We agree. The results of our modifier screen required that we first understand how Tai regulates the Wg pathway before could apply this to understanding the competitive mechanism. Thus, the paper is composed of three sections: 1. the screen, 2. the Tai-Dlp-Wg connection in the absence of competition, and 3. the contribution of Dlp-Wg to the tai[low] ‘loser’ phenotype. These sections use different techniques (e.g., clonal mosaics with genomic alleles, Gal4/UAS and RNAi to define the effect of Tai loss on Wg and Dlp). Ongoing experiments return to clonal mosaics to test whether elevating Dlp can rescue tai lof clones in the same manner as Apc/Apc2 alleles (see Figs. 2-3), which elevate Wg pathway activity.

Specifics:

“It would be good to know whether the authors can rescue tai-low clones by over-expression UAS-Dlp.”

As noted above, experiments are ongoing to test whether normalizing Dlp levels across clonal boundaries rescues elimination of Tai-low clones.

“The data on Wg distribution seems disjointed from the data about cell competition. The authors could refocus the paper to emphasize the cell competition story. The role of Dlp in Wg distribution is well established, so the authors could remove or condense these results. The story really could be Figs 1, 2, 3 and 7 and keep the paper focused on cell competition. The authors could then discuss Dlp as needed for Wg signaling transduction, which is already established in the literature.”

We appreciate the suggestion to reorganize the figures to focus the first part of the story on competition, and then follow with the role of Tai in controlling Dlp. We will consider this approach pending the results of ongoing experiments.  

“The model of tai controlling dlp mRNA and Dlp protein distribution is confusing. In fact, the data for the former is weak, while the data for the latter is strong. I suggest that the authors focus on the altered Dlp protein distribution on tai-low clones. It would also be helpful to prove the Wg signaling is impeded in tai clones (see #5 below).”

We agree but are currently testing how dlp reporters and mRNA respond to Tai in order to rigorously test a Dlp transcriptional mechanism. To complement the ‘strong’ evidence that Tai regulates Dlp distribution, we are testing Dlp in clones of our Tai Crispr null. Since submission, we have also assessed the effect of blocking the endocytic factor shibire/dynamin in Dlp distribution in Tai deficient cells to complement the data on Pentagone that is already in the paper (see Fig. S3).

“I don't know if the Fz3-RFP reported for Wg signaling works in imaginal discs, but if it does then the authors could make clones in this background to prove that cell-autonomous Wg signaling is reduced in tai-low clones.”

We thank the reviewer for this suggestion, which we are now testing.

Reviewer #2

Overall Comments:

“While the authors present good evidence in support of most of their conclusions, there are alternative explanations in many cases that have not been excluded.”

We appreciate this point and are conducting experiments for a revised submission that will help test alternative mechanisms and clarify our conclusions.

Specifics:

“However, the experiments have been done with a single allele, and these experiments do not exclude the possibility that there is another mutation on the same chromosome arm that is responsible for the observed phenotype. Since the authors have a UAS-tai stock, they could strengthen their results using a MARCM experiment where they could test whether the expression of UAS-tai rescues the elimination of tai mutant clones. Alternatively, they could use a second (independent) allele to demonstrate that the phenotype can be attributed to a reduction in tai activity.”

As noted above, we agree with the need for a second allele and are adding supporting data from a new tai lof allele we have generated by Crispr.

The tai[k15101] allele acts as a tai hypomorph and has been shown to produce weaker phenotypes than the 61G1 strong lof in a number of papers (Bai et al, 2000; König et al, 2011, Luo et al, 2019, and Zhang et al, 2015). We agree that rescue of tai[k1501] with a UAS-Tai transgene would help rule out effects of second site mutations. We are currently pursuing the reviewer’s second suggestion of phenocopy with a different allele, our new tai Crispr lof.   

“The authors have screened a total of 21 chromosomes for modification and have not really explained which alleles are nulls and which are hypomorphs. The nature of each of the alleles screened needs to be explained better.”

We will update the text to better reflect what type of alleles were chosen. In most cases we preferred amorphs or null alleles over hypomorphs, however when the amorph option was not available, we used hypomorphs.

“Also, the absence of a dominant modification does not necessarily exclude a function of that gene or pathway in the process. This is especially relevant for the Spz/Toll pathway which the authors have previously implicated in the ability of tai-overexpressing cells to kill wild-type cells.”

We thank the reviewer for this completely accurate point. The dominant screen does not rule out effects of other pathways such as Spz/Toll. Indeed, we were surprised by the lack of dominant effects by Spz/Toll alleles on tai[low] competition given our prior work. The reciprocally clear dominant effect of Apc/Apc2 led us to consider that Wg signaling plays a role in this phenomenon, which then became the starting point of this study.

“The most important discovery from this screen is the modification by the Apc alleles. This part of the paper would be strengthened by testing for modification by other components of the Wingless pathway. The authors show modification by Apc[MI01007] and the double mutant Apc[Q8] Apc2[N175A]. Without showing the Apc[Q8] and Apc2[N175A] alleles separately, it is hard to know if the effect of the double mutant is due to Apc, Apc2,` or the combination.”

We agree that testing for modification with other components of the Wg pathway would be helpful to strengthen the connection between Tai low clonal elimination and Wg pathway biology. We also agree that separating Apc [Q8] and Apc2 [N175A] would be a good idea to check if both Apc proteins are equally important for rescuing Tai low cell death, and future experiments for the lab could investigate this distinction.

“RNAi of tai seems to block the formation of the Wg gradient. If so, one might expect a reduction in wing size. Indeed, this could explain why the wings of tai/Df flies are smaller. The authors mention briefly that the posterior compartment size is reduced when tai-RNAi is expressed in that compartment. However, this observation merits more emphasis since it could explain why tai/Df flies are smaller (Are their wings smaller?).”

We agree that this is an exciting possibility. Growth effects of Tai linked to interactions with Yorkie and EcR could be due to a distinct role in promoting Wg activity. Alternatively, Tai may cooperate with Yorkie or EcR to control Wg pathway. These are exciting possibilities that we are pursuing in future work

With regard to the “small size” effect of reducing Tai, we have previously shown that RNAi of Tai using engrailed-Gal4 causes the posterior compartment to shrink (Zhang et al. 2015, Figure 1C-F, H). In this paper, we also showed that tai[k15101]/Df animals are proportionally smaller than wildtype animals and quantified this by measuring 2D wing size (Zhang et al. 2015, Figure 1A and 1B)

“In Figure 7, the authors show the effect of manipulating Tai levels alone or in combination with increasing Dlp levels. However, they do not include images of Wg protein distribution upon increasing Dlp levels alone.”

We thank the reviewer for this reminder and have already generated these control images to include in a revised submission paper.

“In Figure 8, there is more Wg protein both at the DV boundary and spreading when tai is overexpressed in the source cells using bbg-Gal4. However, in an earlier experiment (Figure 5C) they show that the wg-lacZ reporter is downregulated at the DV boundary when tai is overexpressed using en-Gal4. They therefore conclude that wg is not transcriptionally upregulated but is, instead secreted at higher levels when tai is expressed in the source cells. Wg protein is reduced in the DV stripe with tai is overexpressed using the en-Gal4 driver (Figure 6B') and is increased at the same location when tai is overexpressed with the bbg-Gal4 driver. (Figure 8) I don't know how to reconcile these observations.”

We thank the reviewer for pressing us to develop an overall model explaining our results and how we envision Tai regulating Dlp and Wg. We are preparing a graphic abstract that illustrates this model and will be included in our revision.

Briefly, we favor a model in which Tai controls the rate of Wg spread via Dlp, without a significant effect on wg transcription. For example, the induction of Dlp across the ‘engrailed’ domain of en>Tai discs (Fig 7B-B”) allows Wg to spread rapidly across the flanks and moderately depletes it from the DV margin (Fig 6B-B”) as noted by the reviewer. Adding a UAS-Dlp transgene in the en>Tai background dramatically accelerates Wg spread and causes it to be depleted from the DV margin and build up at the far end of the gradient adjacent to the dorsal and ventral hinge. Significantly blocking endocytosis of Wg in en>Tai discs with a dominant negative shibire transgene also causes Wg to build up in the same location (new data to be added in a revision) consistent with enhanced spreading. The difference in the bbg-Gal4 experiment is that Tai is only overexpressed in DV margin cells, which constrains and concentrates Wg within this restricted domain; we are in the process of testing whether this effect on Wg is blocked by RNAi of Dlp in bbg>Tai discs.

“In Figure 9, the tai-low clones have elevated levels of Dlp. How can this be reconciled with the tai-RNAi knockdown shown in Figure 7C' where reducing tai levels causes a strong reduction in Dlp levels?”

We apologize for not explaining this data well enough. First, the tai[k15101] allele is a weak, viable hypomorph (as shown in our Zhang et al, 2015 paper) whereas the Tai RNAi line is lethal with most drivers (including en-Gal4) and thus a stronger lof. Second, Tai RNAi lower Dlp levels (Fig 7C) while tai[k15101] causes Dlp to accumulate intracellularly (see Fig. 9A-C). These data indicate that reduced Tai leads to a defect in Dlp intracellular trafficking while its loss reduces Dlp overall levels; these data can be explained by a single role for Tai in Dlp traffic to or from the cell membrane, or two roles, one in trafficking and one Dlp expression. As noted, we are investigating both possibilities using dlp reporter lines and our new tai null Crispr allele.

Reviewer #3:

Overall Weaknesses:

“The study has relatively weak evidence for the mechanism of cell competition mediated by Dlp and Wg.”

The screen and middle section of the paper provide genetic evidence that elevating Wg pathway activity rescues Tai[low} loser cells and that Tai controls levels/localization of Dlp and distribution of Wg in the developing wing disc. Our current work is focused on linking these two finding together in Tai “loser” clones.

“More evidence is required to support the claim that dlp transcription or endocytosis is affected in tai clones.”

As noted above, we are testing whether normalizing Dlp levels across clonal boundaries rescues tai[low] loser clones and assessing effects of Tai on dlp transcription and Dlp trafficking.

Specifics:

“Most of the rest of the study is not in the clonal context, and mainly relies on RNAi KD of tai in the posterior compartment, which is a relatively large group of cells. I understand why the authors chose a different approach to investigate the role of tai in cell competition. However because ubiquitous loss of tai results in smaller organs, it is important to determine to what extent reducing levels of tai in the entire posterior compartment compares with clonal elimination i.e. cell competition. This is important in order to determine to what extent the paradigm of Tai-mediated regulation of Dlp levels and by extension, Wg availability, can be extended as a general mechanism underlying competitive elimination of tai-low clones. If the authors want to make a case for mechanisms involved in the competitive elimination of tai clones, then they need to show that the KD of tai in the posterior compartment shows hallmarks of cell competition. Is there cell death along the A/P boundary? Or is the compartment smaller because those cells are growing slower?”

Based on data that cell competition does not occur over compartment boundaries (e.g., see review by L.A. Johnston, Science, 2009), we chose not to use UAS-Gal4 to assess competition, but rather to investigate underlying biology occurring between Tai, Wg, and Dlp.

“Are the levels of Myc/DIAP1, proteins required for fitness, affected in en>tai RNAi cells?”

This is, of course, an interesting question given that Myc is a well-studied competition factor and is proposed to be downstream of the Tai-interacting protein Yki. We are not currently focused on Myc, but plan to test its role in the Tai-Dlp-Wg pathway in future work.

“The authors do not have direct/strong evidence of changes in dlp mRNA levels or intracellular trafficking. To back these claims, the authors should look for dlp mRNA levels and provide more evidence for Dlp endocytosis like an antibody uptake assay or at the very least, a higher resolution image analysis showing a change in the number of intracellular Dlp positive punctae. Also, do the authors think that loss of tai increases Dlp endocytosis, making it less available on the cell surface for maintaining adequate extracellular Wg levels?”

As noted above, have added experiments using a dominant-negative shibire/dynamin allele to test whether Tai controls Dlp endocytosis. These data will be added to a revised manuscript. We have also gathered reagents to test effects of Tai gain/loss on Dlp secretion.

“The data shown in the last figure is at odds with the model (I think) the authors are trying to establish: When cells have lower Tai levels, this reduces Dlp levels (S2) presumably either by reducing dlp transcription and/or increasing (?) Dlp endocytosis. This in turn reduces Wg (availability) in cells away from source cells (Figure 6). The reduced Wg availability makes them less fit, targeting them for competitive elimination. But in tai clones, I do not see any change in cell-surface Dlp (9B) (I would have expected them to be down based on the proposed model). The authors also see more total Dlp (9A) (which is at odds with S2 assuming data in S2 were done under permeabilizing conditions.).”

As noted above (under Rev #2 comments), we apologize for not explaining this data well enough. First, the tai[k15101] allele is a weak, viable hypomorph (as shown in our Zhang et al, 2015 paper) whereas the Tai RNAi line is lethal with most drivers (including en-Gal4) and thus a stronger lof. Second, Tai RNAi lower Dlp levels (Fig 7C) while tai[k15101] causes Dlp to accumulate intracellularly (see Fig. 9A-C). These data indicate that reduced Tai leads to a defect in Dlp intracellular trafficking while its loss reduces Dlp overall levels; these data can be explained by a single role for Tai in Dlp traffic to or from the cell membrane, or two roles, one in trafficking and one Dlp expression. We are investigating both possibilities using dlp reporter lines and our new tai null Crispr allele.

“As a side note, because Dlp is GPI-anchored, the authors should consider the possibility that the 'total' Dlp staining observed in 9A may not be actually total Dlp (and possibly mostly intracellular Dlp, since the permeabilizing membranes with detergent will cause some (most?) Dlp molecules to be lost, and how this might be affecting the interpretation of the data. I think one way to address this would be to process the permeabilized and non-permeabilized samples simultaneously and then image them at the same settings and compare what membrane staining in these two conditions looks like. If membrane staining in the permeabilized condition is decreased compared to non-permeabilized conditions, and the signal intensity of Dlp in permeabilized conditions remains high, then the authors will have evidence to support increased endocytosis in tai clones. Of course, these data will still need to be reconciled with what is shown in S2.

We thank the reviewer for this excellent suggestion and are generating mosaic discs to test the proposed approach of synchronous analysis of total vs. intracellular Dlp.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

(1) A problem with in vitro work is that homogeneous cell lines/cultures are, by nature, absent from the rest of the microenvironment. The authors need to discuss this. 

We have added two sentences to the second paragraph of the Discussion section in which we now acknowledge this concern, but also point out that in vitro models of this sort also provide an experimental advantage in that they facilitate a deconvolution of the extensive complexity resident within the intact animal. Nevertheless, we acknowledge that this deconvolution requires ultimate validation of findings obtained within an in vitro model system to ensure they accurately recapitulate functions that occur in the intact animal in vivo.

(2) What are n's/replicates for each study? Were the same or different samples used to generate the data for RNA sequencing, methylation beadchip analysis, and EM-seq? This clarification is important because if the same cultures were used, this would allow comparisons and correlations within samples.  

Additional text has been added in the Methods section to indicate that all samples involving cell culture models which include iPSCs and PGCLCs came from a single XY iPS cell line aliquoted into replicates and all primary cultures which included Sertoli and granulosa cells were generated from pooled tissue preps from mice and then aliquoted into replicates. Finally, all experiments in the study were performed on three replicates. Because this experimental design did indeed allow for comparisons among samples, we have added a new Supplement figure 9 which displays PCA plots showing clustering among control and treatment datasets, respectively, as well as distinctions between each cluster representing each experimental condition.

(3) In Figure 1, it is interesting that the 50 uM BPS dose mainly resulted in hypermethylation whereas 100 uM appears to be mainly hypomethylation. (This is based on the subjective appearance of graphs). The authors should discuss and/or present these data more quantitatively. For example, what percentage of changes were hypo/hypermethylation for each treatment? How many DMRs did each dose induce? For the RNA-seq results, again, what were the number of up/down-regulated genes for each dose?  

The experiment shown in Figure 1 was designed to 1) serve as proof of principle that cells maintained in culture could be susceptible to EDC-induced epimutagenesis at all, 2) determine if any response observed would be dose-dependent, and 3) identify a minimally effective dose of BPS to be used for the remaining experiments in this study (which we identified as 1 μM). We agree that it is interesting that the 50 µM dose of BPS induced predominantly hypermethylation changes whereas the 1 µM and 100 µM doses induced predominantly hypomethylation changes, but are not in a position to offer a mechanistic explanation for this outcome at this time. As the results shown satisfied our primary objectives of demonstrating that exposure of cells in culture to BPS could indeed induce DNA methylation epimutations, that this occurs in a dose-dependent manner, and that a dose of as low as 1 µM of BPS was sufficient to induce epimutagenesis, the data obtained satisfied all of the initial objectives of this experiment. That said, in response to the reviewer’s request we have now added text on pages 6-7 alluding to new Supplemental tables 1-3 indicating the total number of DMCs and DMRs, as well as the number of DEGs, detected in response to exposure to each dose of BPS shown in Figure 1, as well as stratifying those results to indicate the numbers of hyper- and hypomethylation epimutations and up- and down-regulated DEGs induced in response to each dose of BPS. While, as noted above, investigating the mechanistic basis for the difference in responses induced by the 50 µM versus 1 and 100 µM doses of BPS was beyond the scope of the study presented in this manuscript, we do find this result reminiscent of the “U-shaped” response curves often observed in toxicology studies. Importantly, this result does demonstrate the elevated resolution and specificity of analysis facilitated by our in vitro cell culture model system.

(4) Also in Figure 1, were there DMRs or genes in common across the doses? How did DMRs relate to gene expression results? This would be informative in verifying or refuting expectations that greater methylation is often associated with decreased gene expression.  

In general, we observed a coincidence between changes in DNA methylation and changes in gene expression (Supplement Tables 1-3). Pertaining directly to the reviewer’s question about the extent to which we observed common DMRs and DEGs across all doses, while we only found 3 overlapping DMRs conserved across all doses tested, we did find an average of 51.25% overlap in DMCs and an average of 80.45% overlap in DEGs across iPSCs exposed to the different doses of BPS shown in Figure 1. In addition, within each dose of BPS tested in iPSCs, we also found that there was an overlap between DMCs and the promoters or gene bodies of many DEGs (Supplement Table 4). Specifically within gene promoters, we observed a correlation between hypermethylated DMCs and decreased gene expression and hypomethylated DMCs and increased gene expression, respectively (Supplement Figure 2).

(5) In Figure 2, was there an overlap in the hypo- and/or hyper-methylated DMCs? Please also add more description of the data in 2b to the legend including what the dot sizes/colors mean, etc. Some readers (including me) may not be familiar with this type of data presentation. Some of this comes up in Figure 4, so perhaps allude to this earlier on, or show these data earlier.  

We observed an average of 11.05% overlapping DMCs between different pairs of cell types, we did not observe any DMCs that were shared among all four cell types. Indeed, this limited overlap of DMCs among different cell types exposed to BPS was the primary motivation for the analysis described in Figure 2. Thus, instead of focusing solely on direct overlap between specific DMCs, we instead examined similarities among the different cell types tested in the occurrence of epimutations within different annotated genomic regions. To better describe this, we have now added additional text to page 9. We have also added more detail to the legend for Figure 2 on page 8 to more clearly explain the significance of the dot sizes and colors, explaining that the dot sizes are indicative of the relative number of differentially methylated probes that were detected within each specific annotated genomic region, and that the dot colors are indicative of the calculated enrichment score reflecting the relative abundance of epimutations occurring within a specific annotated genomic region. The relative score is calculated by iterating down the list of DMCs and increasing a running-sum statistic when encountering a DMC within the specific annotated genomic region of interest and decreasing the sum when the epimutation is not in that annotated region. The magnitude of the increment depends upon the relative occurrence of DMCs within a specific annotated genomic region.

(6) iPSCs were derived from male mice MEFs, and subsequently used to differentiate into PGCLCs. The only cell type from an XX female is the granulosa cells. This might be important, and should be mentioned and its potential significance discussed (briefly).  

We have added a new paragraph just before the final paragraph of the Discussion section in which we acknowledge that most of the cell types analyzed during our study were XY-bearing “male” cells and that the manner in which XX-bearing “female” cells might respond to similar exposures could differ from the responses we observed in XY cells. However, we also noted that our assessment of XX-bearing granulosa cells yielded results very similar to those seen in XY Sertoli cells suggesting that, at least for differentiated somatic cell types, there does not appear to be a significant sex-specific difference in response to exposure to a similar dose of the same EDC. That said, we also acknowledged that in cell types in which dosage compensation based on X-chromosome inactivation is not in place, differences between XY- and XX-bearing cells could accrue.

(7) EREs are only one type of hormone response element. The authors make the point that other mechanisms of BPS action are independent of canonical endocrine signaling. Would authors please briefly speculate on the possibility that other endocrine pathways including those utilizing AREs or other HREs may play a role? In other words, it may not be endocrine signaling independent. The statement that the differences between PGCLCs and other cells are largely due to the absence of ERs is overly simplistic.  

Previous reports have indicated that BPS does not have the capacity to bind with the androgen receptor (Pelch et al., 2019; Yang et al., 2024). However there have been reports indicating that BPS can interact with other endocrine receptors including PPARγ and RXRα, which play a role in lipid accumulation and the potential to be linked to obesity phenotypes (Gao et al., 2020; Sharma et al., 2018). To address the reviewer’s comment we assessed the expression of a panel of hormone receptors including PPARγ, RXRα, and AR  in each of the cell types examined in our study and these results are now shown in a new Supplent Figure 4. We show that in addition to not expressing either estrogen receptor (ERa or ERb), germ cells also do not express any of the other endocrine receptors we tested including AR, PPARγ, and RXRα. Thus we now note that these results support our suggestion that the induction of epimutations we observed in germ cells in response to exposure to BPS appears to reflect disruption of non-canonical endocrine signaling. We also note that non-canonical endocrine signaling is well established (Brenker et al., 2018; Ozgyin et al., 2015; Song et al., 2011; Thomas and Dong, 2006). Thus we feel the suggestion that the effects of BPS exposure could conceivably reflect either disruption of canonical or non-canonical signaling in any cell type is well justified and that our data suggests that both of these effects appear to have accrued in the cells examined in our study as suggested in the text of our manuscript.

(8) Interpretation of data from the GO analysis is similarly overly simplistic. The pathways identified and discussed (e.g. PI3K/AKT and ubiquitin-like protease pathways) are involved in numerous functions, both endocrine and non-endocrine. Also, are the data shown in Figure 6a from all 4 cell types? I am confused by the heatmap in 6c, which genes were significantly affected by treatment in which cell types?  

Per the reviewer’s request, we have added text to indicate that Figure 6a is indeed data from all four cell types examined. We have also modified the text to further clarify that Figure 6c displays the expression of other G-coupled protein receptors which are expressed at similar, if not higher, levels than either ER in all cell types examined, and that these have been shown to have the potential to bind to either 17β-estradiol or BPA in rat models. As alluded to by the reviewer, this is indicative of a wide variety of distinct pathways and/or functions that can potentially be impacted by exposure to an EDC such as BPS. Thus, we have attempted to acknowledge the reviewer’s primary point that BPS may interact with a variety of receptors or other factors involved with a wide variety of different pathways and functions. Importantly, this illustrates the strength of our model system in that it can be used to identify potential impacted target pathways that can then be subsequently pursued further as deemed appropriate.

(9) In Figure 7, what were the 138 genes? Any commonalities among them? 

We have now added a new supplemental Excel file that lists the 138 overlapping conserved DEGs that did not become reprogrammed/corrected during the transition from iPSCs to PGCLCs. In addition, we have added new text on page 22 and a new Supplemental Figure 8 which displays KEGG analysis of pathways associated with these 138 retained DEGs. We find that these genes are primarily involved with cell cycle and apoptosis pathways which, interestingly, have the potential to be linked to cancer development which is often linked to disruptions in chromatin architecture.

(10) The Introduction is very long. The last paragraph, beginning line 105, is a long summary of results and interpretations that better fit in a Discussion section.

We have now significantly reduced the length and scope of the final paragraph of the Introduction per the reviewer’s recommendation.

(11) Provide some details on husbandry: e.g. were they bred on-site? What food was given, and how was water treated? These questions are to get at efforts to minimize exposure to other chemicals.  

We have added additional text detailing that all mice used in the project were bred onsite, water was non-autoclaved conventional RO water, and our selection of 5V5R extruded feed for mice used in this study which was highly controlled for the presence of isoflavones and has been certified to be used for estrogen-sensitive animal protocols.

Reviewer #2 (Public Review):

Summary:

This manuscript uses cell lines representative of germ line cells, somatic cells, and pluripotent cells to address the question of how the endocrine-disrupting compound BPS affects these various cells with respect to gene expression and DNA methylation. They find a relationship between the presence of estrogen receptor gene expression and the number of DNA methylation and gene expression changes. Notably, PGCLCs do not express estrogen receptors and although they do have fewer changes, changes are nevertheless detected, suggesting a nonconical pathway for BPS-induced perturbations. Additionally, there was a significant increase in the occurrence of BPS-induced epimutations near EREs in somatic and pluripotent cell types compared to germ cells. Epimutations in the somatic and pluripotent cell types were predominantly in enhancer regions whereas that in the germ cell type was predominantly in gene promoters.

Strengths:

The strengths of the paper include the use of various cell types to address the sensitivity of the lineages to BPS as well as the observed relationship between the presence of estrogen receptors and changes in gene expression and DNA methylation.

Weaknesses:

The weaknesses include the lack of reporting of replicates, superficial bioinformatic analysis, and the fact that exposures are more complicated in a whole organism than in an isolated cell line.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Overall, this is an intriguing paper but more transparency in the replicates and methods and a more rigorous bioinformatic treatment of the data are required.

Specific comments:

(1) End of abstract "These results suggest a unique mechanism by which an EDC-induced epimutated state may be propagated transgenerationally following a single exposure to the causative EDC." This is overly speculative for an abstract. There is only epigenetic inheritance following mitosis or differentiation presented in this study. There is no meiosis and therefore no ability to assess multi- or transgenerational inheritance. 

We have modified the text at the end of the abstract to more precisely reflect our intended conclusions based on our data. In our view, the ability of induced epimutations to transcend meiosis per se is not as relevant to the mechanism of transgenerational inheritance as their ability to transcend major waves of epigenetic reprogramming that normally occur during development of the germ line. In this regard the transition from pluripotent iPSCs to germline PGCLCs has been shown to recapitulate at least the first portion of normal germline reprogramming, and now our data provide novel insight into the fate of induced epimutations during this process. Specifically, we show that a prevelance of epimutations was conserved during the iPSC à germ cell transition but that very few (< 5%) of the specific epimutations present in the the BPS-exposed iPSCs were retained when those cells were induced to form PGCLCs. Rather, we observed apparent correction of a large majority of the initially induced epimutations during this transition, but this was accompanied by the apparent de novo generation of novel epimutations in the PGCLCs. We suggest, based on other recent reports in the literature, that this is a result of the BPS exposure inducing changes in the chromatin architecture in the exposed iPSCs such that when the normal germline reprogramming mechanism is imposed on this disrupted chromatin template there is both correction of many existing epimutations and the genesis of many novel epimutations. This observation has the potential to explain the long-standing question of why the prevalence of epimutations persists across multiple generations despite the occurrence of epigenetic reprogramming during each generation. Nevertheless, as noted above, we have modified the text at the end of the abstract to temper this interpretation given that it is still somewhat speculative at this point.

(2) Doses used in the experiments. One needs to be careful when stating that the dose used is "below FDA's suggested safe environmental level established for BPA" because a different bisphenol is being used here (BPA vs BPS) and the safe level is that which the entire organism experiences. It is likely that cell lines experience a higher effective dose.  

We have now made a point of noting that our reference to an EPA-recommended “safe dose” of BPA was for humans and/or intact animals. Changes to this effect have been made in the second and sixth paragraphs of the Introduction section. In addition, we have added text at the end of the fourth paragraph of the Discussion section acknowledging that, as the reviewer suggests, the same dose of an EDC could exert greater effects on cells in a homogeneous culture than on the same cell type within an intact animal given the potential for mitigating metabolic effects in the latter. However, we also note that the ability we demonstrated to quantify the effects of such exposures on the basis of numbers of epimutations (DMCs or DMRs) induced could potentially be used in future studies to study this question by assessing the effects of a specific dose of a specific EDC on a specific cell type when exposed either within a homogeneous culture or within an intact animal.

(3) Figure 1: In the dose response, what was the overlap in DMCs and DEGs among the 3 doses? Are the responses additive, synergistic, or completely non-overlapping? This is an important point that should be addressed. 

Please see our response to Reviewer 1 critique #4 above where we address similar concerns. While we do find overlap among different cell types with respect to the DMCs, DMRs, and DEGs displayed in Figure 1, we found the effect to be only partially additive as opposed to synergistic in any apparent manner. The fold increase in DMCs, DMRs, and DEGs resulting from exposure to doses of 1 μM or 50 μM ranged from 2.5x to 4.4x, which was well below the 50x increase that would have been expected from a strictly additive effect, and the effect increased even less, if at all, in response to exposure to doses of 50 μM versus 100 μM BPS. Finally, as now noted in the Discussion section on page 25, our conclusion is that these results display a limited dose-dependent effect that was partially additive but also plateaued at the highest doses tested.

(4) Methods: How many times was each exposure performed on a given cell type? This information should be in the figure legends and methods. In the case of multiple exposures for a given line, do the biological replicates agree? 

Please see our response to Reviewer 1 critique #2 where we address similar concerns with newly added text and analysis. We now note repeatedly on pages 39-45 that each analysis was conducted on three replicate samples, and we display the similarity among those replicates graphically in a new Supplement Figure 9.

(5) DNA methylation analyses. Very little analysis is presented on the BeadChip array other than hypermethylated/hypomethylated and genomic regions of DMCs. What is the range of methylation changes? Does it vary between hypo vs. hyper DMCs? How many array experiments were performed (biological replicates) and what stats were used to determine the DMCs? Are there DMCs in common among the various cell types? As an example, if more meaningful analysis, one can plot the %5mC over a given array for comparisons between control and treated cell types. For more granularity, the %5mC can be presented according to the element type (enhancers vs promoters). 

Please see our response to Reviewer 1 critique #2 above where we address similar concerns regarding the number of biological replicates used in this study. DMCs on the Infinium array are identified using mixed linear models. This general supervised learning framework identifies CpG loci at which differential methylation is associated with known control vs. treated co-variates. CpG probes on the array were defined as having differential changes that met both p-value and FDR (≤ 0.05) significant thresholds between treatment and control samples for each cell type analyzed. The range of medians across all samples was 0.0278 to 0.0059 for hypermethylated beta values and -0.0179 to -0.0033 for hypomethylated beta values. As noted above, we did observe an overlap in DMCs between cell types. Thus, we observed an average of 11.05% overlapping DMCs between two or more cell types but we did not observe any DMCs shared between all four cell types. We have added additional text on page 9 and new Supplement Tables 1-4 and Supplement Figure 1 to now more clearly describe that this limited similarity in direct overlap of DMCs was the underlying motivation for the analysis described in Figure 2. Finally, the enrichment dot plots shown in Figure 2 provide the information the reviewer requested regarding the %5mC observed at different annotated genomic element types.

(6) The investigators correlate the number of DMCs in a given cell type with the presence of estrogen receptors. Does the correlation extend to the methylation difference (delta beta) at the statistically different probes?

We have added a new Supplement Figure 3 in which we provide data addressing this question. In brief, we find that the delta betas of probes enriched at enhancer regions and associated with relative proximity to ERE elements in Sertoli cells, granulosa cells, and iPSCs appear very similar to those associated with DMCs not located within these enriched regions. However, when we compared the similarity of the two data sets with goodness of fit tests, we found these relatively small differences were, in fact, statistically significant based on a two-sample Kolmogorov-Smirnov test. These observed significant differences appear to indicate that there is higher variability among the delta betas associated with hypomethylated, but not hypermethylation changes occurring at DMCs associated with enhancers, potentially suggesting a greater tendency for exposure to BPS to induce hypomethylation rather than hypermethylation changes, at least in these specific regions.

(7) Methylation changes relative to EREs are presented in multiple figures. Are other sequences enriched in the DMCs? 

We profiled the genomic sequence within 500 bp of cell type-specific enriched DMCs that were either associated with enhancer regions in Sertoli, granulosa, or iPS cells or transcription factor binding sites in PGCLCs for the identification of higher abundance motif sequences. We then compared any motifs identified with the JASPAR database to potentially find transcription factors that could be binding to these regions. Interestingly we found that the two most common motifs across all cell types were associated with either the chromatin remodeling transcription factor HMG1A or the pluripotency factor KLF4.

(8) Please present a correlation plot between the methylation differences and the adjacent DEGs. Again, the absence of consideration of the absolute changes in methylation and gene expression minimizes the impact of the data. 

We analyzed the relationship between DMCs at DEGs promoter regions and the corresponding change in expression of that DEG. Our data support a relationship between up-regulated genes showing decreased methylation in promoter regions and down-regulated genes showing increased methylation at promoter regions, although there were some exceptions to this relationship.

(9) EM-Seq is mentioned in Figure 7 and in the material and methods. Where is it used in this study? 

We now note in the text on page 22 that EM-seq was used during experiments assessing the propagation of BPS-induced epimutations during the iPSC à EpiLC à PGCLC cell state transitions to gather higher resolution data of changes to DNA methylation differences at the whole-epigenome level.

References

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Author response:

eLife assessment

This manuscript reports an important finding that the transcription factor Scleraxis regulates regenerative myogenesis by controlling the proliferation and differentiation of muscle stem cells. The evidence presented is compelling and supports the conclusions and the mechanisms by which this gene regulates satellite cell function. These data will be of interest to developmental, transcriptional, and stem cell biologists.

Public Reviews:

Reviewer #1 (Public Review):

This manuscript by Bai et al concerns the expression of Scleraxis (Scx) by muscle satellite cells (SCs) and the role of that gene in regenerative myogenesis. The authors report the expression of this gene associated with tendon development in satellite cells. Genetic deletion of Scx in SCs impairs muscle regeneration, and the authors provide evidence that SCs deficient in Scx are impaired in terms of population growth and cellular differentiation. Overall, this report provides evidence of the role of this gene, unexpectedly, in SC function and adult regenerative myogenesis.

We appreciate the comments and thank her/him for the support of our manuscript.

There are a few minor points of concern.

(1) From the data in Figure 1, it appears that all of the SCs, assessed both in vitro and in vivo, express Scx. The authors refer to a scRNA-seq dataset from their lab and one report from mdx mouse muscle that also reveals this unexpected gene expression pattern. Has this been observed in many other scRNA-seq datasets? If not, it would be important to discuss potential explanations as to why this has not been reported previously.

Thanks for this question regarding data in Figure 1. We did initially use immunofluorescence staining of Pax7 and GFP on muscle sections and primary myoblast cultures prepared from Tg-ScxGFP mice to conclude that Scx was expressed in satellite cells (SCs). In addition to the cited mdx RNA-seq data, we have included a re-analysis of a published scRNA-seq data set in Figure 2E (Dell'Orso, Juan et al., Development, 2019), and our own scRNA-seq data (Figure S5D, F). We have also re-examined an additional scRNA-seq data set of TA muscles at various regeneration time points (De Micheli et al., Cell Rep. 2020), in which Scx expression was detected in MuSC progenitors and mature muscle cells (in addition to tenocytes). Thus, our immunostaining results are consistent with scRNA-seq data from our and two other independent scRNA-seq data sets.

We think that Scx expression in the adult myogenic lineage was not previously reported mainly because its expression level was low, and might be dismissed as spurious detection. Additionally, detecting such low expression levels requires sophisticated detection methods with high capture efficiency. Previous studies have noted limitations in transcript capture or transcription factor dropout in 10x Genomics-based datasets (Lambert et al., Cell, 2018; Pokhilko et al., Genome Res., 2021). Or, Scx was simply not a focus in prior studies amid other genes of interest. Our specific focus on Scx has led us to evaluate its expression in these data sets. We will add the above cited scRNA-seq data set (De Micheli et al., Cell Rep. 2020) and provide a discussion in the revised version.

(2) A major point of the paper, as illustrated in Fig. 3, is that Scx-neg SCs fail to produce normal myofibers and renewed SCs following injury/regeneration. They mention in the text that there was no increased PCD by Caspase staining at 5 DPI. A failure of cell survival during the process of SC activation, proliferation, and cell fate determination (differentiation versus self-renewal) would explain most of the in vivo data. As such, this conclusion would seem to warrant a more detailed analysis in terms of at least one or two other time points and an independent method for detecting dead/dying cells (the in vitro data in Fig. 4F is also based on an assessment of activated Caspase to assess cell death). The in vitro data presented later in Fig. S4G, H do suggest an increase in cell loss during proliferative expansion of Scx-neg SCs. To what extent does cell loss (by whatever mechanism of cell death) explain both the in vivo findings of impaired regeneration and even the in vitro studies showing slower population expansion in the absence of Scx?

We appreciate these constructive suggestions. Additional methods and different time points should be helpful in investigating SC cell loss in ScxcKO. Based on the number of available cKO animals, we will carefully choose additional time point(s) to assess PCD, using anti-active Caspase-3 immunostaining and another independent method (e.g., TUNNEL). Although the outcomes are uncertain, we will endeavor to obtain meaningful data from these experiments.

(3) I'm not sure I understand the description of the data or the conclusions in the section titled "Basement membrane-myofiber interaction in control and Scx cKO mice". Is there something specific to the regeneration from Scx-neg myogenic progenitors, or would these findings be expected in any experimental condition in which myogenesis was significantly delayed, with much smaller fibers in the experimental group at 5 DPI?

We very much appreciate this comment. We agree that there is unlikely anything specific about the regeneration from Scx-negative myogenic progenitors. Unfilled or empty ghost fibers (basement membrane remnant) are to be expected due to the small fiber and poor regeneration in the ScxcKO mice at 5 dpi. We will correct the subtitle and content accordingly.

(4) The data presented in Fig. 4B showing differences in the purity of SC populations isolated by FACS depending on the reporter used are interesting and important for the field. The authors offer the explanation of exosomal transfer of Tdt from SCs to non-SCs. The data are consistent with this explanation, but no data are presented to support this. Are there any other explanations that the authors have considered and that could be readily tested?

Thanks for highlighting this phenomenon. We struggled with the SC purity issue for a long time. The project started with using the R26RtdT reporter for tdT’s paraformaldehyde  resistant strong fluorescence (fixation) to aid visualization in vivo. Later, when we used the tdT signal to purify SCs by FACS, we found that only 80% sorted tdT+ cells are Pax7+. We then switched to the R26RYFP reporter, from which we achieved much higher purity (95%) of SCs (Pax7+) by FACS. As such, we also repeated and confirmed many in vivo experimental results using the R26RYFP reporter (included in the manuscript). Due to the low purity of tdT+SCs by FACS, we discontinued that mouse colony after we confirmed the superior utility of the R26RYFP reporter for SC isolation.

We sincerely apologize for not being able to conduct further testable experiments on this intriguing phenomenon. However, this issue has since been addressed and published by Murach et al., iScience, (2021). Like our experience, they found non-satellite mononuclear cells with tdT fluorescence after TMX treatment when SCs were isolated via FACS. To determine this was not due to off-target recombination or a technical artifact from tissue processing, they conducted extensive analyses. They found that the tdT+ mononuclear cells included fibrogenic cells (fibroblasts and FAPs), immune cells/macrophages, and endothelial cells. Additionally, they confirmed the significant potential of extracellular vesicle (EV)-mediated cargo transfer, which facilitates the transfer of full-length tdT transcript from lineage-marked Pax7+ cells to those mononuclear cells. We will modify our text to include and acknowledge their contribution to this important point.

(5) The Cut&Run data of Fig. 6 certainly provide evidence of direct Scx targets, especially since the authors used a novel knock-in strain for analyses. The enrichment of E-box motifs provides support for the 207 intersecting genes (scRNA-seq and Cut&Run) being direct targets. However, the rationale elaborated in the final paragraph of the Results section proposing how 4 of these genes account for the phenotypes on the Scx-neg cells and tissues is just speculation, however reasonable. These are not data, and these considerations would be more appropriate in the Discussion in the absence of any validation studies.

We agree with this comment and will move this speculation into the discussion.

Reviewer #2 (Public Review):

Summary:

Scx is a well-established marker for tenocytes, but the expression in myogenic-lineage cells was unexplored. In this study, the authors performed lineage-trace and scRNA-seq analyses and demonstrated that Scx is expressed in activated SCs. Further, the authors showed that Scx is essential for muscle regeneration using conditional KO mice and identified the target genes of Scx in myogenic cells, which differ from those of tendons.

Strengths:

Sometimes, lineage-trace experiments cause mis-expression and do not reflect the endogenous expression of the target gene. In this study, the authors carefully analyzed the unexpected expression of Scx in myogenic cells using some mouse lines and scRNA-seq data.

We appreciate the comments and thank her/him for noting the strengths of our manuscript.

Weaknesses:

Scx protein expression has not been verified.

We are aware of this weakness. We had previously used Western blotting (WB) using cultured SCs from control and ScxcKO mice, but did not detect endogenous Scx protein in the control. Hence, we used ScxCreERT2 lineage-tracing, Tg-ScxGFP expression, and ScxTy1 knock-in allele as complementary, even though indirect, ways to address this issue. Following the reviewer’s comment, we will purchase new anti-Scx antibodies and re-perform WB using cultured SCs. If the new antibodies fail to detect endogenous Scx by WB, we will then use immunofluorescence staining to detect endogenous Scx protein.

Author response:

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

eLife assessment

This study provides valuable information on the mechanism of PepT2 through enhanced-sampling molecular dynamics, backed by cell-based assays, highlighting the importance of protonation of selected residues for the function of a proton-coupled oligopeptide transporter (hsPepT2). The molecular dynamics approaches are convincing, but with limitations that could be addressed in the manuscript, including lack of incorporation of a protonation coordinate in the free energy landscape, possibility of protonation of the substrate, errors with the chosen constant pH MD method for membrane proteins, dismissal of hysteresis emerging from the MEMENTO method, and the likelihood of other residues being affected by peptide binding. Some changes to the presentation could be considered, including a better description of pKa calculations and the inclusion of error bars in all PMFs. Overall, the findings will appeal to structural biologists, biochemists, and biophysicists studying membrane transporters.

We would like to express our gratitude to the reviewers for providing their feedback on our manuscript, and also for recognising the variety of computational methods employed, the amount of sampling collected and the experimental validation undertaken. Following the individual reviewer comments, as addressed point-by-point below, we have prepared a revised manuscript, but before that we address some of the comments made above in the general assessment:

• “lack of incorporation of a protonation coordinate in the free energy landscape”.

We acknowledge that of course it would be highly desirable to treat protonation state changes explicitly and fully coupled to conformational changes. However, at this point in time, evaluating such a free energy landscape is not computationally feasible (especially considering that the non-reactive approach taken here already amounts to almost 1ms of total sampling time).  Previous reports in the literature tend to focus on either simpler systems or a reduced subset of a larger problem.  As we were trying to obtain information on the whole transport cycle, we decided to focus here on non-reactive methods.

• “possibility of protonation of the substrate”.

The reviewers are correct in pointing out this possibility, which we had not discussed explicitly in our manuscript.  Briefly, while we describe a mechanism in which protonation of only protein residues (with an unprotonated ligand) can account for driving all the necessary conformational changes of the transport cycle, there is some evidence for a further intermediate protonation site in our data (as we commented on in the first version of the manuscript as well), which may or may not be the substrate itself. A future explicit treatment of the proton movements through the transporter, when it will become computationally tractable to do so, will have to include the substrate as a possible protonation site; for the present moment, we have amended our discussion to alert the reader to the possibility that the substrate could be an intermediate to proton transport. This has repercussions for our study of the E56 pKa value, where – if protons reside with a significant population at the substrate C-terminus – our calculated shift in pKa upon substrate binding could be an overestimate, although we would qualitatively expect the direction of shift to be unaffected. However, we also anticipate that treating this potential coupling explicitly would make convergence of any CpHMD calculation impractical to achieve and thus it may be the case that for now only a semi-quantitative conclusion is all that can be obtained.

• “errors with the chosen constant pH MD method for membrane proteins”.

We acknowledge that – as reviewer #1 has reminded us – the AMBER implementation of hybrid-solvent CpHMD is not rigorous for membrane proteins, and as such added a cautionary note to our paper.  We also explain how the use of the ABFE thermodynamic cycle calculations helps to validate the CpHMD results in a completely orthogonal manner (we have promoted this validation, which was in the supplementary figures, into the main text in the revised version).   We therefore remain reasonably confident in the results presented with regards to the reported pKa shift of E56 upon substrate binding, and suggest that if the impact of neglecting the membrane in the implicit-solvent stage of CpHMD is significant, then there is likely an error cancellation when considering shifts induced by the incoming substrate.

• “dismissal of hysteresis emerging from the MEMENTO method”.

We have shown in our method design paper how the use of the MEMENTO method drastically reduces hysteresis compared to steered MD for path generation, and find this improvement again for PepT2 in this study. We address reviewer #3’s concern about our presentation on this point by revising our introduction of the MEMENTO method, as detailed in the response below.

• “the likelihood of other residues being affected by peptide binding”.

In this study, we have investigated in detail the involvement of several residues in proton-coupled di-peptide transport by PepT2. Short of the potential intermediate protonation site mentioned above, the set of residues we investigate form a minimal set of sorts within which the important driving forces of alternating access can be rationalised.  We have not investigated in substantial detail here the residues involved in holding the peptide in the binding site, as they are well studied in the literature and ligand promiscuity is not the problem of interest here. It remains entirely possible that further processes contribute to the mechanism of driving conformational changes by involving other residues not considered in this paper. We have now made our speculation that an ensemble of different processes may be contributing simultaneously more explicit in our revision, but do not believe any of our conclusions would be affected by this.

As for the additional suggested changes in presentation, we provide the requested details on the CpHMD analysis. Furthermore, we use the convergence data presented separately in figures S12 and S16 to include error bars on our 1D-reprojections of the 2D-PMFs in figures 3, 4 and 5. (Note that we have opted to not do so in figures S10 and S15 which collate all 1D PMF reprojections for the OCC ↔ OF and OCC ↔ IF transitions in single reference plots, respectively, to avoid overcrowding those necessarily busy figures). We have also changed the colours schemes of these plots in our revision to improve accessibility. We have additionally taken the opportunity to fix some typos and further clarified some other statements throughout the manuscript, besides the requests from the reviewers.

Reviewer #1 (Public Review):

The authors have performed all-atom MD simulations to study the working mechanism of hsPepT2. It is widely accepted that conformational transitions of proton-coupled oligopeptide transporters (POTs) are linked with gating hydrogen bonds and salt bridges involving protonatable residues, whose protonation triggers gate openings. Through unbiased MD simulations, the authors identified extra-cellular (H87 and D342) and intra-cellular (E53 and E622) triggers. The authors then validated these triggers using free energy calculations (FECs) and assessed the engagement of the substrate (Ala-Phe dipeptide). The linkage of substrate release with the protonation of the ExxER motif (E53 and E56) was confirmed using constant-pH molecular dynamics (CpHMD) simulations and cellbased transport assays. An alternating-access mechanism was proposed. The study was largely conducted properly, and the paper was well-organized. However, I have a couple of concerns for the authors to consider addressing.

We would like to note here that it may be slightly misleading to the reader to state that “The linkage of substrate release with the protonation of the ExxER motif (E53 and E56) was confirmed using constant-pH molecular dynamics (CpHMD) simulations and cell-based transport assays.” The cellbased transport assays confirmed the importance of the extracellular gating trigger residues H87, S321 and D342 (as mentioned in the preceding sentence), not of the substrate-protonation link as this line might be understood to suggest.

(1) As a proton-coupled membrane protein, the conformational dynamics of hsPepT2 are closely coupled to protonation events of gating residues. Instead of using semi-reactive methods like CpHMD or reactive methods such as reactive MD, where the coupling is accounted for, the authors opted for extensive non-reactive regular MD simulations to explore this coupling. Note that I am not criticizing the choice of methods, and I think those regular MD simulations were well-designed and conducted. But I do have two concerns.

a) Ideally, proton-coupled conformational transitions should be modelled using a free energy landscape with two or more reaction coordinates (or CVs), with one describing the protonation event and the other describing the conformational transitions. The minimum free energy path then illustrates the reaction progress, such as OCC/H87D342-  →  OCC/H87HD342H →  OF/H87HD342H as displayed in Figure 3.

We concur with the reviewer that the ideal way of describing the processes studied in our paper would be as a higher-dimensional free energy landscapes obtained from a simulation method that can explicitly model proton-transfer processes. Indeed, it would have been particularly interesting and potentially informative with regards to the movement of protons down into the transporter in the OF → OCC → IF sequence of transitions. As we note in our discussion on the H87→E56 proton transfer: 

“This could be investigated using reactive MD or QM/MM simulations (both approaches have been employed for other protonation steps of prokaryotic peptide transporters, see Parker et al. (2017) and Li et al. (2022)).  However, the putative path is very long (≈ 1.7 nm between H87 and E56) and may or may not involve a large number of intermediate protonatable residues, in addition to binding site water. While such an investigation is possible in principle, it is beyond the scope of the present study.” 

Where even sampling the proton transfer step itself in an essentially static protein conformation would be pushing the boundaries of what has been achieved in the field, we believe that considering the current state-of-the-art, a fully coupled investigation of large-scale conformational changes and proton-transfer reaction is not yet feasible in a realistic/practical time frame. We also note this limitation already when we say that:

“The question of whether proton binding happens in OCC or OF warrants further investigation, and indeed the co-existence of several mechanisms may be plausible here”. 

Nonetheless, we are actively exploring approaches to treat uptake and movement of protons explicitly for future work.

In our revision, we have expanded on our discussion of the reasoning behind employing a non-reactive approach and the limitations that imposes on what questions can be answered in this study.

Without including the protonation as a CV, the authors tried to model the free energy changes from multiple FECs using different charge states of H87 and D342. This is a practical workaround, and the conclusion drawn (the OCC→ OF transition is downhill with protonated H87 and D342) seems valid. However, I don't think the OF states with different charge states (OF/H87D342-, OF/H87HD342-, OF/H87D342H, and OF/H87HD342H) are equally stable, as plotted in Figure 3b. The concern extends to other cases like Figures 4b, S7, S10, S12, S15, and S16. While it may be appropriate to match all four OF states in the free energy plot for comparison purposes, the authors should clarify this to ensure readers are not misled.

The reviewer is correct in their assessment that the aligning of PMFs in these figures is arbitrary; no relative free energies of the PMFs to each other can be estimated without explicit free energy calculations at least of protonation events at the end state basins. The PMFs in our figures are merely superimposed for illustrating the differences in shape between the obtained profiles in each condition, as discussed in the text, and we now make this clear in the appropriate figure captions.

b) Regarding the substrate impact, it appears that the authors assumed fixed protonation states. I am afraid this is not necessarily the case. Variations in PepT2 stoichiometry suggest that substrates likely participate in proton transport, like the Phe-Ala (2:1) and Phe-Gln (1:1) dipeptides mentioned in the introduction. And it is not rigorous to assume that the N- and C-termini of a peptide do not protonate/deprotonate when transported. I think the authors should explicitly state that the current work and the proposed mechanism (Figure 8) are based on the assumption that the substrates do not uptake/release proton(s).

This is indeed an assumption inherent in the current work. While we do “speculate that the proton movement processes may happen as an ensemble of different mechanisms, and potentially occur contemporaneously with the conformational change” we do not in the previous version indicate explicitly that this may involve the substrate. We make clear the assumption and this possibility in the revised version of our paper. Indeed, as we discuss, there is some evidence in our PMFs of an additional protonation site not considered thus far, which may or may not be the substrate. We now make note of this point in the revised manuscript.

As for what information can be drawn from the given experimental stoichiometries, we note in our paper that “a 2:1 stoichiometry was reported for the neutral di-peptide D-Phe-L-Ala and 3:1 for anionic D-Phe-L-Glu. (Chen et al., 1999) Alternatively, Fei et al. (1999) have found 1:1 stoichiometries for either of D-Phe-L-Gln (neutral), D-Phe-L-Glu (anionic), and D-Phe-L-Lys (cationic).” 

We do not assume that it is our place to arbit among the apparent discrepancies in the experimental data here, although we believe that our assumed 2:1 stoichiometry is additionally “motivated also by our computational results that indicate distinct and additive roles played by two protons in the conformational cycle mechanism”.

(2) I have more serious concerns about the CpHMD employed in the study.

a) The CpHMD in AMBER is not rigorous for membrane simulations. The underlying generalized Born model fails to consider the membrane environment when updating charge states. In other words, the CpHMD places a membrane protein in a water environment to judge if changes in charge states are energetically favorable. While this might not be a big issue for peripheral residues of membrane proteins, it is likely unphysical for internal residues like the ExxER motif. As I recall, the developers have never used the method to study membrane proteins themselves. The only CpHMD variant suitable for membrane proteins is the membrane-enabled hybrid-solvent CpHMD in CHARMM. While I do not expect the authors to redo their CpHMD simulations, I do hope the authors recognize the limitations of their method.

We discuss the limitations of the AMBER CpHMD implementation in the revised version. However, despite that, we believe we have in fact provided sufficient grounds for our conclusion that substrate binding affects ExxER motif protonation in the following way.

In addition to CpHMD simulations, we establish the same effect via ABFE calculations, where the substrate affinity is different at the E56 deprotonated vs protonated protein. This was figure S20 before, though in the revised version we have moved this piece of validation into a new panel of figure 6 in the main text, since it becomes more important with the CpHMD membrane problem in mind. Since the ABFE calculations are conducted with an all-atom representation of the lipids and the thermodynamic cycle closes well, it would appear that if the chosen CpHMD method has a systematic error of significant magnitude for this particular membrane protein system, there may be the benefit of error cancellation. While the calculated absolute pKa values may not be reliable, the difference made by substrate binding appears to be so, as judged by the orthogonal ABFE technique.

Although the reviewer does “not expect the authors to redo their CpHMD simulations”, we consider that it may be helpful to the reader to share in this response some results from trials using the continuous, all-atom constant pH implementation that has recently become available in GROMACS (Aho et al 2022, https://pubs.acs.org/doi/10.1021/acs.jctc.2c00516) and can be used rigorously with membrane proteins, given its all-atom lipid representation.

Unfortunately, when trying to titrate E56 in this CpHMD implementation, we found few protonationstate transitions taking place, and the system often got stuck in protonation state–local conformation coupled minima (which need to interconvert through rearrangements of the salt bridge network involving slow side-chain dihedral rotations in E53, E56 and R57). Author response image 1 shows this for the apo OF state, Author response image 2 shows how noisy attempts at pKa estimation from this data turn out to be, necessitating the use of a hybrid-solvent method.

Author response image 1.

All-atom CpHMD simulations of apo-OF PepT2. Red indicates protonated E56, blue is deprotonated.

Author response image 2.

Difficulty in calculating the E56 pKa value from the noisy all-atom CpHMD data shown in Author response image 1.

b) It appears that the authors did not make the substrate (Ala-Phe dipeptide) protonatable in holosimulations. This oversight prevents a complete representation of ligand-induced protonation events, particularly given that the substrate ion pairs with hsPepT2 through its N- & C-termini. I believe it would be valuable for the authors to acknowledge this potential limitation. 

In this study, we implicitly assumed from the outset that the substrate does not get protonated, which – as by way of response to the comment above – we now acknowledge explicitly. This potential limitation for the available mechanisms for proton transfer also applies to our investigation of the ExxER protonation states. In particular, a semi-grand canonical ensemble that takes into account the possibility of substrate C-terminus protonation may also sample states in which the substrate is protonated and oriented away from R57, thus leaving the ExxER salt bridge network in an apo-like state. The consequence would be that while the direction of shift in E56 pKa value will be the same, our CpHMD may overestimate its magnitude. It would thus be interesting to make the C-terminus protonatable for obtaining better quantitative estimates of the E56 pKa shift (as is indeed true in general for any other protein protonatable residue, though the effects are usually assumed to be negligible). We do note, however, that convergence of the CpHMD simulations would be much harder if the slow degree of freedom of substrate reorientation (which in our experience takes 10s to 100s of nanoseconds in this binding pocket) needs to be implicitly equilibrated upon protonation state transitions. We discuss such considerations in the revised paper.

Reviewer #2 (Public Review):

This is an interesting manuscript that describes a series of molecular dynamics studies on the peptide transporter PepT2 (SLC15A2). They examine, in particular, the effect on the transport cycle of protonation of various charged amino acids within the protein. They then validate their conclusions by mutating two of the residues that they predict to be critical for transport in cell-based transport assays. The study suggests a series of protonation steps that are necessary for transport to occur in Petp2. Comparison with bacterial proteins from the same family shows that while the overall architecture of the proteins and likely mechanism are similar, the residues involved in the mechanism may differ. 

Strengths: 

This is an interesting and rigorous study that uses various state-of-the-art molecular dynamics techniques to dissect the transport cycle of PepT2 with nearly 1ms of sampling. It gives insight into the transport mechanism, investigating how the protonation of selected residues can alter the energetic barriers between various states of the transport cycle. The authors have, in general, been very careful in their interpretation of the data. 

Weaknesses: 

Interestingly, they suggest that there is an additional protonation event that may take place as the protein goes from occluded to inward-facing but they have not identified this residue.

We have indeed suggested that there may be an additional protonation site involved in the conformational cycle that we have not been able to capture, which – as we discuss in our paper – might be indicated by the shapes of the OCC ↔ IF PMFs given in Figure S15. One possibility is for this to be the substrate itself (see the response to reviewer #1 above) though within the scope of this study the precise pathway by which protons move down the transporter and the exact ordering of conformational change and proton transfer reactions remains a (partially) open question. We acknowledge this, denote it with question marks in the mechanistic overview we give in Figure 8 and also “speculate that the proton movement processes may happen as an ensemble of different mechanisms, and potentially occur contemporaneously with the conformational change”.

Some things are a little unclear. For instance, where does the state that they have defined as occluded sit on the diagram in Figure 1a? - is it truly the occluded state as shown on the diagram or does it tend to inward- or outward-facing?

Figure 1a is a simple schematic overview intended to show which structures of PepT2 homologues are available to use in simulations. This was not meant to be a quantitative classification of states. Nonetheless, we can note that the OCC state we derived has extra- and intracellular gate opening distances (as measured by the simple CVs defined in the methods and illustrated in Figure 2a) that indicate full gate closure at both sides. In particular, although it was derived from the IF state via biased sampling, the intracellular gate opening distance in the OCC state used for our conformational change enhanced sampling was comparable to that of the OF state (ie, full closure of the gate), see Figure S2b and the grey bars therein. Therefore, we would schematically classify the OCC state to lie at the center of the diagram in Figure 1a. Furthermore, it is largely stable over triplicates of 1 μslong unbiased MD, where in 2/3 replicates the gates remain stable, and the remaining replicate there is partial opening of the intracellular gate (as shown in Figure 2 b/c under the “apo standard” condition). We comment on this in the main text by saying that “The intracellular gate, by contrast, is more flexible than the extracellular gate even in the apo, standard protonation state”, and link it to the lower barrier for transition to IF than to OF. We did this by saying that “As for the OCC↔OF transitions, these results explain the behaviour we had previously observed in the unbiased MD of Figure 2c.” We acknowledge this was not sufficiently clear and have added details to the latter sentence to help clarify better the nature of the occluded state.

The pKa calculations and their interpretation are a bit unclear. Firstly, it is unclear whether they are using all the data in the calculations of the histograms, or just selected data and if so on what basis was this selection done. Secondly, they dismiss the pKa calculations of E53 in the outward-facing form as not being affected by peptide binding but say that E56 is when there seems to be a similar change in profile in the histograms.

In our manuscript, we have provided two distinct analyses of the raw CpHMD data. Firstly, we analysed the data by the replicates in which our simulations were conducted (Figure 6, shown as bar plots with mean from triplicates +/- standard deviation), where we found that only the effect on E56 protonation was distinct as lying beyond the combined error bars. This analysis uses the full amount of sampling conducted for each replicate. However, since we found that the range of pKa values estimated from 10ns/window chunks was larger than the error bars obtained from the replicate analysis (Figures S17 and S18), we sought to verify our conclusion by pooling all chunk estimates and plotting histograms (Figure S19). We recover from those the effect of substrate binding on the E56 protonation state on both the OF and OCC states. However, as the reviewer has pointed out (something we did not discuss in our original manuscript), there is a shift in the pKa of E53 of the OF state only. In fact, the trend is also apparent in the replicate-based analysis of Figure 6, though here the larger error bars overlap. In our revision, we added more details of these analyses for clarity (including more detailed figure captions regarding the data used in Figure 6) as well as a discussion of the partial effect on the E53 pKa value. 

We do not believe, however, that our key conclusions are negatively affected. If anything, a further effect on the E53 pKa which we had not previously commented on (since we saw the evidence as weaker, pertaining to only one conformational state) would strengthen the case for an involvement of the ExxER motif in ligand coupling.

Reviewer #3 (Public Review):

Summary: 

Lichtinger et al. have used an extensive set of molecular dynamics (MD) simulations to study the conformational dynamics and transport cycle of an important member of the proton-coupled oligopeptide transporters (POTs), namely SLC15A2 or PepT2. This protein is one of the most wellstudied mammalian POT transporters that provides a good model with enough insight and structural information to be studied computationally using advanced enhanced sampling methods employed in this work. The authors have used microsecond-level MD simulations, constant-PH MD, and alchemical binding free energy calculations along with cell-based transport assay measurements; however, the most important part of this work is the use of enhanced sampling techniques to study the conformational dynamics of PepT2 under different conditions. 

The study attempts to identify links between conformational dynamics and chemical events such as proton binding, ligand-protein interactions, and intramolecular interactions. The ultimate goal is of course to understand the proton-coupled peptide and drug transport by PepT2 and homologous transporters in the solute carrier family. 

Some of the key results include:

(1) Protonation of H87 and D342 initiate the occluded (Occ) to the outward-facing (OF) state transition. 

(2) In the OF state, through engaging R57, substrate entry increases the pKa value of E56 and thermodynamically facilitates the movement of protons further down. 

(3) E622 is not only essential for peptide recognition but also its protonation facilitates substrate release and contributes to the intracellular gate opening. In addition, cell-based transport assays show that mutation of residues such as H87 and D342 significantly decreases transport activity as expected from simulations. 

Strengths: 

(1) This is an extensive MD-based study of PepT2, which is beyond the typical MD studies both in terms of the sheer volume of simulations as well as the advanced methodology used. The authors have not limited themselves to one approach and have appropriately combined equilibrium MD with alchemical free energy calculations, constant-pH MD, and geometry-based free energy calculations. Each of these 4 methods provides a unique insight regarding the transport mechanism of PepT2.

(2) The authors have not limited themselves to computational work and have performed experiments as well. The cell-based transport assays clearly establish the importance of the residues that have been identified as significant contributors to the transport mechanism using simulations.

(3) The conclusions made based on the simulations are mostly convincing and provide useful information regarding the proton pathway and the role of important residues in proton binding, protein-ligand interaction, and conformational changes.

Weaknesses: 

(1) Some of the statements made in the manuscript are not convincing and do not abide by the standards that are mostly followed in the manuscript. For instance, on page 4, it is stated that "the K64-D317 interaction is formed in only ≈ 70% of MD frames and therefore is unlikely to contribute much to extracellular gate stability." I do not agree that 70% is negligible. Particularly, Figure S3 does not include the time series so it is not clear whether the 30% of the time where the salt bridge is broken is in the beginning or the end of simulations. For instance, it is likely that the salt bridge is not initially present and then it forms very strongly. Of course, this is just one possible scenario but the point is that Figure S3 does not rule out the possibility of a significant role for the K64-D317 salt bridge. 

The reviewer is right to point out that the statement and Figure S3 as they were do not adequately support our decision to exclude the K64-D317 salt-bridge in our further investigations. The violin plot shown in Figure S3, visualised as pooled data from unbiased 1 μs triplicates, did indeed not rule out a scenario where the salt bridge only formed late in our simulations (or only in some replicates), but then is stable. Therefore, in our revision, we include the appropriate time-series of the salt bridge distances, showing how K64-D317 is initially stable but then falls apart in replicate 1, and is transiently formed and disengaged across the trajectories in replicates 2 and 3. We have also remade the data for this plot as we discovered a bug in the relevant analysis script that meant the D170-K642 distance was not calculated accurately. The results are however almost identical, and our conclusions remain.

(2) Similarly, on page 4, it is stated that "whether by protonation or mutation - the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed (Figure S5)." I do not agree with this assessment. The authors need to be aware of the limitations of this approach. Consider "WT H87-prot" and "D342A H87-prot": when D342 residue is mutated, in one out of 3 simulations, we see the opening of the gate within 1 us. When D342 residue is not mutated we do not see the opening in any of the 3 simulations within 1 us. It is quite likely that if rather than 3 we have 10 simulations or rather than 1 us we have 10 us simulations, the 0/3 to 1/3 changes significantly. I do not find this argument and conclusion compelling at all.

If the conclusions were based on that alone, then we would agree.  However, this section of work covers merely the observations of the initial unbiased simulations which we go on to test/explore with enhanced sampling in the rest of the paper, and which then lead us to the eventual conclusions.

Figure S5 shows the results from triplicate 1 μs-long trajectories as violin-plot histograms of the extracellular gate opening distance, also indicating the first and final frames of the trajectories as connected by an arrow for orientation – a format we chose for intuitively comparing 48 trajectories in one plot. The reviewer reads the plot correctly when they analyse the “WT H87-prot” vs “D342A H87-prot” conditions. In the former case, no spontaneous opening in unbiased MD is taking place, whereas when D342 is mutated to alanine in addition to H87 protonation, we see spontaneous transition in 1 out of 3 replicates.  However, the reviewer does not seem to interpret the statement in question in our paper (“the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed”) in the way we intended it to be understood. We merely want to note here a correlation in the unbiased dataset we collected at this stage, and indeed the one spontaneous opening in the case comparison picked out by the reviewer is in the condition where both the H87 interaction network and D342-R206 are perturbed. In noting this we do not intend to make statistically significant statements from the limited dataset. Instead, we write that “these simulations show a large amount of stochasticity and drawing clean conclusions from the data is difficult”. We do however stand by our assessment that from this limited data we can “already appreciate a possible mechanism where protons move down the transporter pore” – a hypothesis we investigate more rigorously with enhanced sampling in the rest of the paper. We have revised the section in question to make clearer that the unbiased MD is only meant to give an initial hypothesis here to be investigated in more detail in the following sections. In doing so, we also incorporate, as we had not done before, the case (not picked out by the reviewer here but concerning the same figure) of S321A & H87 prot. In the third replicate, this shows partial gate opening towards the end of the unbiased trajectory (despite D342 not being affected), highlighting further the stochastic nature that makes even clear correlative conclusions difficult to draw.

(3) While the MEMENTO methodology is novel and interesting, the method is presented as flawless in the manuscript, which is not true at all. It is stated on Page 5 with regards to the path generated by MEMENTO that "These paths are then by definition non-hysteretic." I think this is too big of a claim to say the paths generated by MEMENTO are non-hysteretic by definition. This claim is not even mentioned in the original MEMENTO paper. What is mentioned is that linear interpolation generates a hysteresis-free path by definition. There are two important problems here: (a) MEMENTO uses the linear interpolation as an initial step but modifies the intermediates significantly later so they are no longer linearly interpolated structures and thus the path is no longer hysteresisfree; (b) a more serious problem is the attribution of by-definition hysteresis-free features to the linearly interpolated states. This is based on conflating the hysteresis-free and unique concepts. The hysteresis in MD-based enhanced sampling is related to the presence of barriers in orthogonal space. For instance, one may use a non-linear interpolation of any type and get a unique pathway, which could be substantially different from the one coming from the linear interpolation. None of these paths will be hysteresis-free necessarily once subjected to MD-based enhanced sampling techniques.

We certainly do not intend to claim that the MEMENTO method is flawless. The concern the reviewer raises around the statement "These paths are then by definition non-hysteretic" is perhaps best addressed by a clarification of the language used and considering how MEMENTO is applied in this work. 

Hysteresis in the most general sense denotes the dependence of a system on its history, or – more specifically – the lagging behind of the system state with regards to some physical driver (for example the external field in magnetism, whence the term originates). In the context of biased MD and enhanced sampling, hysteresis commonly denotes the phenomenon where a path created by a biased dynamics method along a certain collective variable lags behind in phase space in slow orthogonal degrees of freedom (see Figure 1 in Lichtinger and Biggin 2023, https://doi.org/10.1021/acs.jctc.3c00140). When used to generate free energy profiles, this can manifest as starting state bias, where the conformational state that was used to seed the biased dynamics appears lower in free energy than alternative states. Figure S6 shows this effect on the PepT2 system for both steered MD (heavy atom RMSD CV) + umbrella sampling (tip CV) and metadynamics (tip CV). There is, in essence, a coupled problem: without an appropriate CV (which we did not have to start with here), path generation that is required for enhanced sampling displays hysteresis, but the refinement of CVs is only feasible when paths connecting the true phase space basins of the two conformations are available. MEMENTO helps solve this issue by reconstructing protein conformations along morphing paths which perform much better than steered MD paths with respect to giving consistent free energy profiles (see Figure S7 and the validation cases in the MEMENTO paper), even if the same CV is used in umbrella sampling. 

There are still differences between replicates in those PMFs, indicating slow conformational flexibility propagated from end-state sampling through MEMENTO. We use this to refine the CVs further with dimensionality reduction (see the Method section and Figure S8), before moving to 2D-umbrella sampling (figure 3). Here, we think, the reviewer’s point seems to bear. The MEMENTO paths are ‘non-hysteretic by definition’ with respect to given end states in the sense that they connect (by definition) the correct conformations at both end-states (unlike steered MD), which in enhanced sampling manifests as the absence of the strong starting-state bias we had previously observed (Figure S7 vs S6). They are not, however, hysteresis-free with regards to how representative of the end-state conformational flexibility the structures given to MEMENTO really were, which is where the iterative CV design and combination of several MEMENTO paths in 2D-PMFs comes in. 

We also cannot make a direct claim about whether in the transition region the MEMENTO paths might be separated from the true (lower free energy) transition paths by slow orthogonal degrees of freedom, which may conceivably result in overestimated barrier heights separating two free energy basins. We cannot guarantee that this is not the case, but neither in our MEMENTO validation examples nor in this work have we encountered any indications of a problem here.

We hope that the reviewer will be satisfied by our revision, where we replace the wording in question by a statement that the MEMENTO paths do not suffer from hysteresis that is otherwise incurred as a consequence of not reaching the correct target state in the biased run (in some orthogonal degrees of freedom).

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors): 

Figure S1: it would be useful to label the panels.

We have now done this.

At the bottom of page 4, it is written that "the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed (Figure S5)." But it is hard to interpret that from the figure.  

See also our response to reviewer #3. We have revised the wording of this statement, and also highlight in Figure S5 the crucial runs we are referring to, in order to make them easier to discern.

At the bottom of page 5, and top of page 6, there is a lot of "other" information shown, which is inserted for the record - this is a bit glossed over and hard to follow.

The “other” information refers to further conditions we had calculated PMFs for and that gave some insight, but which were secondary for drawing our key conclusions. We thank the reviewer for their feedback that this section needs clarification. We have revised this paragraph to make it easier to follow and highlight better the conclusions we draw form the data.

In Figure 7 it looks as though the asterisks have shifted.

We are indebted to the reviewer for spotting this error, the asterisks are indeed shifted one bar to the right of their intended position. The revised version fixes this issue.

Reviewer #3 (Recommendations For The Authors):

Minor points: In Figure 1a, The 7PMY label and arrow are slightly misplaced.

Figure 1a is a schematic diagram to show the available structures of PepT2 homologues (see also the response to reviewer #2 above). The 7PMY label placement is intentional to indicate a partially occluded inwards-facing state. As we write in the figure caption: “Intermediate positions between states indicate partial gate opening”.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

TMC7 knockout mice were generated by the authors and the phenotype was analyzed. They found that Tmc7 is localized to Golgi and is needed for acrosome biogenesis.

Strengths:

The phenotype of infertility is clear, and the results of TMC7 localization and the failed acrosome formation are highly reliable. In this respect, they made a significant discovery regarding spermatogenesis.

Weaknesses:

There are also some concerns, which are mainly related to the molecular function of TMC7 and Figure 5.

(1) It is understandable that TMC7 exhibits some channel activity in the Golgi and somehow affects luminal pH or Ca2+, leading to the failure of acrosome formation. On the other hand, since they are conducting the pH and calcium imaging from the cytoplasm, I do not think that the effect of TMC7 channel function in Golgi is detectable with their methods.

We agree with the reviewer that there are no direct evidences showing the effect of TMC7 channel function in Golgi. We have changed the description in the revised manuscript.

(2) Rather, it is more likely that they are detecting apoptotic cells that have no longer normal ion homeostasis.

We thank the reviewer for raising this concern. We apologize for not labeling the postnatal stage in original Figure 5. We measured intracellular Ca2+, pH and ROS in PD30 testes (revised Fig. S6a-c), no apoptotic cells were observed at this stage (revised Fig. S6e, f). Apoptotic cells were found in the seminiferous tubules and cauda epididymis of 9-week-old Tmc7–/– mice (revised Fig. 5e-f). We have included TUNEL data in testis of PD21, PD30 and 9-week-old mice (revised Fig. 5e, f and Fig. S6e, f). In accordance with our findings, Tmc1 mutation has also been shown to result in reduced Ca2+ permeability, thus triggering hair cell apoptosis (Fettiplace, R, PNAS. 2022) [1].

(3) Another concern is that n is only 3 for these imaging experiments.

As suggested by the reviewer, more replicates were included in imaging experiments.

Reviewer #2 (Public Review):

Summary:

This study presents a significant finding that enhances our understanding of spermatogenesis. TMC7 belongs to a family of transmembrane channel-like proteins (TMC1-8), primarily known for their role in the ear. Mutations to TMC1/2 are linked to deafness in humans and mice and were originally characterized as auditory mechanosensitive ion channels. However, the function of the other TMC family members remains poorly characterized. In this study, the authors begin to elucidate the function of TMC7 in acrosome biogenesis during spermatogenesis. Through analysis of transcriptomics datasets, they identify TMC7 as a transmembrane channel-like protein with elevated transcript levels in round spermatids in both mouse and human testis. They then generate Tmc7-/- mice and find that male mice exhibit smaller testes and complete infertility. Examination of different developmental stages reveals spermatogenesis defects, including reduced sperm count, elongated spermatids, and large vacuoles. Additionally, abnormal acrosome morphology is observed beginning at the early-stage Golgi phase, indicating TMC7's involvement in proacrosomal vesicle trafficking and fusion. They observed localization of TMC7 in the cis-Golgi and suggest that its presence is required for maintaining Golgi integrity, with Tmc7-/- leading to reduced intracellular Ca2+, elevated pH, and increased ROS levels, likely resulting in spermatid apoptosis. Overall, the work delineates a new function of TMC7 in spermatogenesis and the authors suggest that its ion channel activity is likely important for Golgi homeostasis. This work is of significant interest to the community and is of high quality.

Strengths:

The biggest strength of the paper is the phenotypic characterization of the TMC7-/- mouse model, which has clear acrosome biogenesis/spermatogenesis defects. This is the main claim of the paper and it is supported by the data that are presented.

Weaknesses:

The claim is that TMC7 functions as an ion channel. It is reasonable to assume this given what has been previously published on the more well-characterized TMCs (TMC1/2), but the data supporting this is preliminary here, and more needs to be done to solidify this hypothesis. The authors are careful in their interpretation and present this merely as a hypothesis supporting this idea.

We appreciate the insightful comment. It is indeed a limitation of our study that we lack strong evidences to support that TMC7 functions as an ion channel. We have planned to conduct cellular electrophysiology in GC-1 cells heterologous expression of TMC7. However, TMC7 was trapped in the endoplasmic reticulum like TMC1 and TMC2 (Yu X, PNAS. 2020)[2], and failed to localize to the Golgi. According to the reviewer’s suggestion, we have made careful and more detailed interpretation the molecular function of TMC7 in the revised manuscript.

Reviewer #3 (Public Review):

Summary:

In this study, Wang et al. have demonstrated that TMC7, a testis-enriched multipass transmembrane protein, is essential for male reproduction in mice. Tmc7 KO male mice are sterile due to reduced sperm count and abnormal sperm morphology. TMC7 co-localizes with GM130, a cis-Golgi marker, in round spermatids. The absence of TMC7 results in reduced levels of Golgi proteins, elevated abundance of ER stress markers, as well as changes of Ca2+ and pH levels in the KO testis. However, further confirmation is required because the analyses were performed with whole testis samples in spite of the differences in the germ cell composition in WT and KO testis. In addition, the causal relationships between the reported anomalies await thorough interrogation.

Strengths:

The microscopic images are of great quality, all figures are properly arranged, and the entire manuscript is very easy to follow.

Weaknesses:

(1) Tmc7 KO male mice show multiple anomalies in sperm production and morphogenesis, such as reduced sperm count, abnormal sperm head, and deformed midpiece. Thus, it is confusing that the authors focused solely on impaired acrosome biogenesis.

We are grateful to your comments and suggestions. We agree and have added these defects in spermiogenesis of Tmc7–/– mice in the abstract and discussion sections of revised manuscript.

(2) Further investigations are warranted to determine whether the abnormalities reported in this manuscript (e.g., changes in protein, Ca2+, and pH levels) are directly associated with the molecular function of TMC7 or are the byproducts of partially arrested spermiogenesis. Please find additional comments in "Recommendations for the authors".

Thank you for raising this concern. Per your comments, we have included data of intracellular Ca2+, pH and ROS in PD21 testes. The intracellular homeostasis was impaired as early as PD21, indicating TMC7 depletion impairs cellular homeostasis which in turn results in arrested spermiogenesis.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

As noted by all three reviewers, current flow cytometry data does not necessarily support the 'ion channel' hypothesis, thus the phenotypic analysis is compelling but the molecular mechanism of how TMC7 facilitates acrosome biogenesis remains incomplete. It is highly recommended for the authors to at least discuss or test alternative hypotheses (as reviewer #2 suggested) such as the possibility of acting as 'lipid scramblase'. Also, the authors need to provide further explanation for other morphological defects if TMC7 is truly a functional ion channel in Golgi (and thus later at acrosome), which is also related to the key question of whether TMC7 is a functional ion channel.

We thank the reviewing editor for the comments and suggestions. We agree that our study lack strong evidences to support that TMC7 functions as an ion channel. We have discussed the possibility of TMC7 acting as 'lipid scramblase' as suggested. We have also included data of intracellular Ca2+, pH and ROS in PD21, PD30 testes.

Indeed, Tmc7–/– mice exhibits other defects including abnormal head morphology and disorganized mitochondrial sheaths. As TMC7 is localized to the cis-Golgi apparatus and is required for maintaining Golgi integrity. Previous studies on Golgi localized proteins including GOPC (Yao R, PNAS. 2002)[2], HRB (Kang-Decker N. Science. 2001)[3] and PICK1(Xiao N, JCI. 2009)[4] exhibit similar defects in spermiogenesis with Tmc7–/– mice. It is possible that defects morphologies in Tmc7–/– mice might be due to impaired function of Golgi.

Reviewer #1 (Recommendations For The Authors):

(1) The authors should provide more details about the imaging experiments using FACS. Since they only describe catalog numbers (Beyotime, S1056, S1006, S0033S) for imaging reagents, it is not immediately clear what reagents they actually used. Since they used Fluo3, BCECF, and DCFH, it would be better to mention their names.

Thanks. We have provided more detailed antibody information as suggested.

(2) I am also concerned that in the FACS there is no information at all about laser wavelength and filter properties. This is especially important for BCECF because the wavelength spectrum changes with pH. Also, if there are any positive controls for these imaging reagents, such as ionophores, it would be more convincing to include them.

Thank you for your comment. Excitation wavelength is 488nm for detecting Ca2+, pH and ROS in FACS. BCECF is the most popular pH probe to monitor cellular pH and the reagent from Beyotime (S1006) has been used by other studies (Chen S, Blood. 2016)[5], (Liu H, Cell Death Dis. 2022)[6]. To make the results more reliable, we have repeated these experiments in PD21 testes (revised Figure 5a-c). No positive controls for these reagents were used in our experiments.

(3) As noted above, it is better to avoid directly linking the cell's abnormal ion homeostasis to TMC7 ion channel function in the text. The discussion should be changed to emphasize that the TMC7-deficient cells are apoptotic and that these physiological phenomena are occurring as a side effect of this apoptosis.

Thank you for raising this concern. We agree with the reviewer that there are no direct evidences showing the effect of TMC7 channel function in Golgi and we have changed the description in the revised manuscript.

We performed new experiment to measure apoptosis and intracellular Ca2+, pH and ROS in PD21 testes. No apoptotic cells were observed at this stage. However, impaired cellular homeostasis was still found in testis of PD21 Tmc7-/- mice. These data suggest that TMC7 depletion impairs cellular homeostasis and hence induces spermatid apoptosis.

(4) While I understand that it appears to be difficult to experimentally verify the ion channel function of TMC7, it may be supportive to compare its amino acid sequence and/or 3D predicted structure with that of TMC1/2. Including a supplemental figure for this purpose would emphasize the possibility that TMC7 functions as an ion channel.

We thank the reviewer for making this great suggestion. We compared the amino acid sequence and structure of TMC1, TMC2 with TMC7 respectively. TMC1 had 81% sequence similarity with TMC7 and the RMSD (Root Mean Square Deviation) was 3.079. TMC2 had 82% sequence similarity with TMC7, the RMSD was 2.176. These data suggest that TMC7 has similar amino acid sequence and predicted structure with TMC1/2 and might functions as an ion channel. We have included the predicted structures in revised Fig. S7.

Author response image 1.

Reviewer #2 (Recommendations For The Authors):

I do not have any experimental comments or concerns to address, but I do ask that the authors consider an alternative hypothesis. Based on prior data demonstrating that TMC1 is a mechanosensitive ion channel, the authors reasonably assume that TMC7 may also function as an ion channel. Although the authors observe alterations in cytosolic Ca2+ and pH upon loss of TMC7 by flow cytometry, which begins to support this hypothesis, these data do not directly demonstrate ion channel activity.

I was wondering if the authors had considered whether TMC7 could also function as a lipid scramblase. TMC1 has also been proposed to function as a Ca2+-inhibited scramblase, where knockout of TMC1 leads to a loss of phosphatidylserine (PS) exposure and membrane blebbing at the apical region of hair cells (Ballesteros, A. and Swartz, K., Science Advances, 2022). Furthermore, TMC proteins are structurally related to the Anoctamin/TMEM16 family of chloride channels and lipid scramblases, where TMEM16A-B are bona fide Ca2+-activated chloride channels, and TMEM16C-H are characterized as Ca2+-dependent scramblases. Based on their structural similarity and the observation that TMC1 may also exhibit lipid scrambling properties based on the PS exposure, I wonder if the authors may have data that support a TMC7 scramblase hypothesis. I was intrigued by this idea, especially given the authors' observations of large vacuoles in the seminiferous tubules and cauda epididymis and the vesicle accumulation phenotype in their TEM data. Incorporating this hypothesis into the discussion section, at minimum, could provide a valuable perspective, and this line of thought may lead to interesting data interpretation throughout the paper.

We thank the reviewer for the valuable suggestion. We have discussed the possibility of TMC7 acting as 'lipid scramblase' as suggested.

Reviewer #3 (Recommendations For The Authors):

(1) Gene symbols should be italicized, and protein symbols should be capitalized.

Thanks. We have made changes to the manuscript as recommended.

(2) Tmc7 KO males show reduced sperm count, which alters the germ cell composition in the testis (Figure 2g). Thus, it is inappropriate to compare protein levels using whole testis lysates (Figure 3e, 4h, 5d, 5f). Instead, the same immunoblotting analyses could be done with purified round spermatids or 3-wk-old testis. Likewise, the significance of the intracellular Ca2+ and pH measurements is potentially diminished by the differences in the germ cell composition in WT and KO mice.

We appreciate this constructive suggestion. We agree with the reviewer that whole testis lysates diminished the differences between WT and _Tmc7-/-_mice. However, we are unable purify round spermatids due to the lack of specific markers.

(3) Figures 2i, 2j: How sperm motility was measured should be specified in the Methods.

We thank you for your significant reminding and have added sperm motility assessment in Methods section.

(4) Figure 4g: It does not make sense to compare the fluorescence intensity of these proteins without making sure that the seminiferous tubules are in the same stage. As shown in Figures S5a and S5b, TMC7 exhibits varied abundance in spermatids at different steps.

We thank the reviewer for the insightful comment. We have replaced images in the same stage seminiferous tubules and compared the fluorescence intensity of new images as suggested.

(5) Figure 4h: How were the band intensities measured? The third band from the left is visually stronger than the first one, but it does not seem to be so according to the column graph. The reviewer measured the intensity of GRASP65 bands relative to alpha-tubulin by ImageJ and obtained relative intensities of 0.35, 0.87, 0.6, and 0.08 for the bands from left to right. Additional replicates of the western blots should be included in the supplementary figures.

Thank you for this insightful comment. The density and size of the blots were quantified by Image J. We have checked the first band from the left of GRASP65 and it seems that the protein was not fully transferred onto the PVDF membrane. We have performed new experiments and replaced the original bands (Revised Fig. 4h). Additional replicates of the western blots have been included in revised Fig. S8.

(6) Figures 5a, 5b: Based on the observation of abnormal intracellular Ca2+ and pH levels in the KO germ cells, the authors concluded that TMC7 maintains the homeostasis of Golgi pH and ion (Lines 223-224, 263-264). However, intracellular Ca2+ and pH levels do not directly reflect those in the Golgi apparatus.

We thank the reviewer for this important comment. We agree and have changed “Golgi” to “intracellular” as suggested.

(7) Figure 5c: ROS is produced during apoptosis. Thus, it is not appropriate to conclude that the increased ROS levels in Tmc7 KO germ cells lead to apoptosis.

According to the reviewer’s comment, we measured ROS and apoptosis in testis of PD21 and PD30 mice. ROS levels were increased, but no apoptotic cells were observed in testis of PD21 and PD30 Tmc7–/– mice. Apoptotic cells were observed in testis of 9-week-old Tmc7–/– mice (Revised Fig. 5e-f). These data suggest that TMC7 depletion results in the accumulation of ROS, thereby leads to apoptosis.

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Author response:

eLife assessment:

This manuscript reports valuable findings on the role of the Srs2 protein in turning off the DNA damage signaling response initiated by Mec1 (human ATR) kinase. The data provide solid evidence that Srs2 interaction with PCNA and ensuing SUMO modification is required for checkpoint downregulation. However, experimental evidence with regard to the model that Srs2 acts at gaps after camptothecin-induced DNA damage is currently lacking. The work will be of interest to cell biologists studying genome integrity but would be strengthened by considering the possible role of Rad51 and its removal. 

We appreciate the editors and the reviewers for providing evaluation and helpful comments. As detailed below, we plan to adjust the writing and figures to address the points raised by the reviewers. We believe that these changes will improve the clarity of the work. Below is a summary of our plan to address the two main criticisms.

(1) Regarding the sites of Srs2 action, our data support the conclusion that Srs2 removal of RPA is favored at a subset of ssDNA regions that have proximal PCNA, but not at sites lacking PCNA. A logical supposition for the former types of ssDNA regions includes ssDNA gaps and tails generated during DNA repair or replication, wherein PCNA can be loaded at the ssDNA-dsDNA junction with a 3’ DNA end. Examples of the latter type of ssDNA regions without proximal PCNA can form within negatively supercoiling regions or intact R-loops, both of which lack 3’ DNA end for PCNA loading. While we have stated this conclusion in the text, we highlighted ssDNA gaps as sites of Srs2 action in Discussion and in the model figure, which could be misleading. We will clarify our model, that is, Srs2 distinguishes among different types of ssDNA regions using PCNA proximity as a guide for RPA removal, and state that the precise nature of Srs2 action sites remain to be determined. Regardless, the feature of Srs2 revealed in this work provides a rationale for how it can remove RPA at subsets of ssDNA regions without unnecessary stripping of RPA at other sites.

(2) While Rad51 removal is an important facet of Srs2 functions, it is not relevant to our current study based on the following observations and rationales.

First, we have provided several lines of evidence to support the conclusion that Rad51 removal by Srs2 is separable from the Srs2-RPA antagonism (Dhingra et al., 2021). For example, while rad51∆ rescues the hyper-recombination phenotype of srs2∆ cells, it does not affect the hyper-checkpoint phenotype of srs2∆. Strikingly, rfa1-zm1/zm2 have the opposite effect. The differential effects of rad51∆ and rfa1-zm1/zm2 were also seen for the srs2-_ATPase dead allele (_srs2-K41A). For example, rfa1-zm2 rescued the hyper-checkpoint defect and the CPT sensitivity of srs2-K41A, while rad51∆ had neither effect.

These and other data described in Dhingra et al suggest that Srs2’s effects on checkpoint vs. recombination are separable and that the Srs2-RPA antagonism during the DNA damage checkpoint is independent of Rad51.

Second, our current work addresses which Srs2 features affect the Srs2-RPA antagonism during the DNA damage response and its implications. Given this antagonism is separable from Srs2 removal of Rad51, including Rad51 regulation would be distractive from the main points of this work.

Third, in the current work, we began by examining all known regulatory and protein-protein interaction features of Srs2, including the Rad51 binding domain. Consistent with our conclusion summarized above based on the Dhingra et al study, deleting the Rad51 binding domain in Srs2 (srs2-∆Rad51BD) has no effect on rfa1-zm2 phenotype in CPT (Figure 2D). This is in sharp contrast to mutating the PCNA binding and the sumoylation sites of Srs2, which suppressed rfa1-zm2 for its CPT sensitivity and checkpoint abnormalities (Figure 2C). This data provides yet another evidence that Srs2 regulation of Rad51 is separable from the Srs2-RPA antagonism. 

In summary, our work provides a foundation for future examination of how Srs2 regulates RPA and Rad51 in different manners, how these two facets of the Srs2 functions affect genome integrity in different capacity, and whether there is a crosstalk between them during certain DNA metabolism processes.

Public Reviews:

Reviewer #1:

Overall, the data presented in this manuscript is of good quality. Understanding how cells control RPA loading on ssDNA is crucial to understanding DNA damage responses and genome maintenance mechanisms. The authors used genetic approaches to show that disrupting PCNA binding and SUMOylation of Srs2 can rescue the CPT sensitivity of rfa1 mutants with reduced affinity for ssDNA. In addition, the authors find that SUMOylation of Srs2 depends on binding to PCNA and the presence of Mec1. Noted weaknesses include the lack of evidence supporting that Srs2 binding to PCNA and its SUMOylation occur at ssDNA gaps, as proposed by the authors. Also, the mutants of Srs2 with impaired binding to PCNA or impaired SUMOylation showed no clear defects in checkpoint dampening, and in some contexts, even resulted in decreased Rad53 activation. Therefore, key parts of the paper would benefit from further experimentation and/or clarification.  

We thank the reviewer for the positive comments on this work and address her/his remark regarding ssDNA gaps below in Major Comment #1. In addition, we detailed below our data and rationale in suggesting that the checkpoint dampening phenotype of srs2-∆PIM and -3KR (deficient for PCNA binding and sumoylation, respectively) is masked by redundant pathways. We further describe our plan to enhance the clarity of both text and model to address these points from the reviewer. 

Major Comments 

(1) The central model proposed by the authors relies on the loading of PCNA at the 3' junction of an ssDNA gap, which then mediates Srs2 recruitment and RPA removal. While several aspects of the model are consistent with the data, the evidence that it is occurring at ssDNA gaps is not strong. The experiments mainly used CPT, which generates mostly DSBs. The few experiments using MMS, which mostly generates ssDNA gaps, show that Srs2 mutants lead to weaker rescue in this context (Figure S1). How do the authors explain this discrepancy? In the context of DSBs, are the authors proposing that Srs2 is engaging at later steps of HRdriven DSB repair where PCNA gets loaded to promote fill-in synthesis? If so, is RPA removal at that step important for checkpoint dampening? These issues need to be addressed and the final model adjusted. 

We appreciate the reviewer’s concern. Our conclusion is that Srs2 can be guided by PCNA to a subset of ssDNA regions for RPA removal, and that this Srs2 action is not favored at ssDNA regions with no proximal PCNA. It is important to note that CPT can produce both types of ssDNA regions. Besides ssDNA generated via DSB-associated recombinational repair, CPT can also lead to ssDNA gap formation upon excision repair and DNA-protein crosslink repair of trapped Top1 (Sun et al., 2020). ssDNA regions generated during these DNA repair processes often contain 3’ DNA end for PCNA loading, thus they can favor Srs2 removal of RPA. Another facet of CPT’s effects (besides DNA lesions) is depleting functional pool of Top1, thus causing topological stress and consequently increased levels of DNA supercoiling and R-loops (Koster et al., 2007, Petermann et al., 2022). ssDNA formed within the negatively supercoiled regions and in R-loops lacks 3’ DNA end unless it is cleaved by nucleases, thus these sites would be disfavored for Srs2 removal of RPA due to lack of PCNA loading. Our conclusion that ssDNA regions with nearby PCNA are preferred sites for Srs2 action provides a rationale for how Srs2 can remove RPA at certain ssDNA regions but minimize unnecessary stripping of RPA from other sites.

We will clarify in Discussion that CPT can generate twp types of ssDNA regions as stated above, and that Srs2 could distinguish among them using PCNA proximity as a guide for RPA removal. While this conclusion was described in the text, we emphasized ssDNA gap as a Srs2 action site in the model. We will clarify that while this is a logical supposition, other types of ssDNAs with proximal PCNA could also be targeted by Srs2 and that our work paves the way to determine the precise nature of ssDNA regions for Srs2’s action. 

The reasons for the less potent growth suppression of rfa1 mutants by srs2 alleles in MMS condition compared with CPT condition are unclear, but multiple possibilities should be considered, given that MMS and CPT affect checkpoint responses differently and that RPA and Srs2 affect growth in multiple ways. For example, while CPT only activates the DNA damage checkpoint, MMS additionally induces DNA replication checkpoint (Menin et al., 2018, Redon et al., 2003). It is thus possible that the Srs2-RPA antagonism is relatively more important for the DNA damage checkpoint than the DNA replication checkpoint. Further investigation of this possibility among others will shed light on differential suppressive effects seen in this work. We will include this discussion in the revised text.

(2) The data in Figure 3 showing that Srs2 mutants reduce Rad53 activation in the rfa1-zm2 mutant are confusing, especially given the claim of an anti-checkpoint function for Srs2 (in which case Srs2 mutants should result in increased Rad53 activation). The authors propose that Rad53 is hyperactivated in rfa1-zm2 mutant because of compromised ssDNA protection and consequential DNA lesions, however, the effects sharply contrast with the central model. Are the authors proposing that in the rfa1-zm2 mutant, the compromised protection of ssDNA supersedes the checkpoint-dampening effect? Perhaps a schematic should be included in Figure 3 to depict these complexities and help the reader. The schematic could also include the compensatory dampening mechanisms like Slx4 (on that note, why not move Figure S2 to a main figure?... and even expand experiments to better characterize the compensatory mechanisms, which seem important to help understand the lack of checkpoint dampening effect in the Srs2 mutants) 

Genetic interactions that involve partially defective alleles, multi-functional proteins, and redundant pathways are complex to comprehend. For example, a phenotype seen for the null allele may not be seen for partially defective alleles. In the context of this study, while srs2 null increased Rad53 activation (Dhingra et al., 2021), srs2-∆PIM and -3KR did not (Figure 3A-3B). However, srs2-∆PIM enhanced Rad53 activation when combined with another checkpoint dampening mutant slx4RIM, suggesting that defects of srs2-∆PIM can be compensated by Slx4 (Figure S2). Importantly, srs2-∆PIM and -3KR rescued rfa1-zm2’s checkpoint abnormality (Figure 3A3B), suggesting that Srs2 binding to PCNA and its sumoylation contribute to the Srs2-RPA antagonism in the DNA damage checkpoint response.

A partially defective allele that impairs a specific function of a protein can be a powerful genetic tool even when it lacks a particular phenotype on its own. For example, a partially defective allele of the checkpoint protein Rad9 impairing its binding to gamma-H2A (rad9-K1088M) does not affect the G2/M checkpoint nor cause DNA damage sensitivity due to the compensation of other checkpoint factors (Hammet et al., 2007); however_, rad9-K1088M_ rescues the DNA damage sensitivity and persistent G2/M checkpoint of rtt107 and slx4 mutants, providing one of the evidences supporting a role of the Slx4-Rtt107 axis in removal of Rad9 from chromatin (via competing with Rad9 for gamma-H2A binding) (Ohouo et al., 2013).

In order to highlight the checkpoint recovery process, the model in Figure 6 did not depict another consequence of the Srs2-RPA antagonism. In the presence of Srs2, DNA binding rfa1 mutants can lead to increased levels of DNA lesions and checkpoint, and these defects are rescued by lessening Srs2’s ability to strip RPA from DNA (Dhingra et al., 2021). We will modify the model in Figure 6 and its legend to clarify that the model depicts just one of the consequences of the Srs2 and RPA antagonism with a focus on the checkpoint recovery. We will also state these points more clearly in the Discussion. Further, a new schematic in Figure 3 as suggested by the reviewer will be added to outline the genetic relationship and interpretation. We will also follow reviewer’s suggestion to move Figure S2 to the main figures. Better characterizing the compensatory mechanisms among different checkpoint dampening pathways is very interesting but requires substantial amounts of work. While it is beyond the scope of the current study, it could be pursued in the future.

(3) The authors should demarcate the region used for quantifying the G1 population in Figure 3B and explain the following discrepancy: By inspection of the cell cycle graph, all mutants have lower G1 peak height compared to WT (CPT 2h). However, in the quantification bar graph at the bottom, ΔPIM has higher G1 population than the WT. 

We have added the description on how the G1 region of the FACS histogram was selected to derive the percentage of G1 cells in Figure 3B. Briefly, for samples collected for a particular strain, the G1 region of the “G1 sample” was used to demarcate the G1 region of the “CPT 2h” sample. Upon re-checking the included FACS profiles, we realized that a mutant panel and its datapoint were mistakenly put in the place for wild-type. We will correct this mistake. The conclusion remains that srs2-∆PIM and srs2-3KR improved rfa1-zm2 cells’ ability to exit G2/M, while they themselves do not show difference from the wild-type control for the percentage of G1 cells after 2hr CPT treatment. We will add statistics in figures to reflect this conclusion and adjust the order of strains shown in panel A and B to be consistent with each other.

Reviewer #2:

This is an interesting paper that delves into the post-translational modifications of the yeast Srs2 helicase and proteins with which it interacts in coping with DNA damage. The authors use mutants in some interaction domains with RPA and Srs2 to argue for a model in which there is a balance between RPA binding to ssDNA and Srs2's removal of RPA. The idea that a checkpoint is being regulated is based on observing Rad53 and Rad9 phosphorylation (so there are the attributes of a checkpoint), but evidence of cell cycle arrest is lacking. The only apparent delay in the cell cycle is the re-entry into the second S phase (but it could be an exit from G2/M); but in any case, the wild-type cells enter the next cell cycle most rapidly. No direct measurement of RPA residence is presented. 

We thank the reviewer for the helpful comments. Previous studies have shown that CPT does not induce the DNA replication checkpoint, thus it does not slow down or arrest S phase progression; however, CPT does induce the DNA damage checkpoint, which causes a delay of G2/M cells to re-enter into the second cell cycle (Menin et al., 2018, Redon et al., 2003). Our result is consistent with previous findings, showing that CPT induces G2/M delay but not arrest. We will adjust the text to make this point clearer.

We have previously reported chromatin-bound RPA levels in rfa1-zm2, srs2, and their double mutants, as well as in vitro ssDNA binding by wild-type and mutant RPA complexes (Dhingra et al., 2021). We found that Srs2 loss or its ATPase dead mutant led to 4-6 fold increase of RPA levels on chromatin, which was rescued by rfa1-zm2 (Dhingra et al., 2021). On its own, rfa1-zm2 did not cause defective chromatin association in our assays, despite modestly reducing ssDNA binding in vitro (Dhingra et al., 2021). This discrepancy could be due to a lack of sensitivity of chromatin fractionation assay in revealing moderate changes of RPA residence on DNA. Considering this, we decided to employ functional assays (Figure 2-3) that are more effective in identifying the Srs2 features pertaining to RPA regulation. 

Strengths:

Data concern viability assays in the presence of camptothecin and in the post-translational modifications of Srs2 and other proteins.

Weaknesses:

There are a couple of overriding questions about the results, which appear technically excellent. Clearly, there is an Srs2-dependent repair process here, in the presence of camptothecin, but is it a consequence of replication fork stalling or chromosome breakage? Is repair Rad51-dependent, and if so, is Srs2 displacing RPA or removing Rad51 or both? If RPA is removed quickly what takes its place, and will the removal of RPA result in lower DDC1-MEC1 signaling? 

While Srs2 can affect both the checkpoint response and DNA repair in CPT conditions, the rfa1-zm2 allele, which affects the former but not the latter, role of Srs2, allows us to gain a deeper understanding of the former role (Dhingra et al., 2021). This role also appears to be critical for cell survival in CPT, since srs2∆ growth on CPT-containing media was greatly improved by rfa1-zm mutants (Dhingra et al., 2021). Building on this understanding, our current study identified two Srs2 features that could afford spatial and temporal regulations of RPA removal from DNA, thus providing a rationale for how cells can properly utilize this beneficial yet also dangerous activity. Study of Srs2-mediated repair in CPT conditions, either in Rad51-dependent or independent manner, before and after replication forks stall or DNA breaks, will require substantial efforts and can be pursued in the future. We will add this point to the revised manuscript.

Moreover, it is worth noting that in single-strand annealing, which is ostensibly Rad51 independent, a defect in completing repair and assuring viability is Srs2-dependent, but this defect is suppressed by deleting Rad51. Does deleting Rad51 have an effect here? 

We have shown in our previous paper (Dhingra et al., 2021). that rad51∆ did not rescue the hyper-checkpoint phenotype of srs2∆ cells in CPT condition (Dhingra et al., 2021), while rfa1-zm1 and -zm2 did (Dhingra et al., 2021). Such differential effects were also seen for the srs2 ATPase-dead allele (Dhingra et al., 2021). These and other data described in the Dhingra et al paper suggest that Srs2’s effects on checkpoint vs. recombination are separable at least in CPT condition, and that the Srs2-RPA antagonism in checkpoint regulation is not affected by Rad51 removal (unlike in SSA situation).

Neither this paper nor the preceding one makes clear what really is the consequence of having a weakerbinding Rfa1 mutant. Is DSB repair altered? Neither CPT nor MMS are necessarily good substitutes for some true DSB assay. 

In our previous report (Dhingra et al., 2021), we showed that the rfa1-zm mutants did not affect the frequencies of rDNA recombination, gene conversation, or direct repeat repair (Dhingra et al., 2021). Further, rfa1-zm mutants did not suppress the hyper-recombination phenotype of srs2∆, while rad51∆ did (Dhingra et al., 2021). In a DSB system, wherein the direct repeats flanking the break were placed 30 kb away from each other, srs2∆ led to hyper-checkpoint and lethality, both of which were rescued by rfa1-zm mutants (Dhingra et al., 2021). In this assay, rfa1-zm mutants themselves did not show sensitivity, suggesting the repair is largely proficient. Collectively, these data provide evidence to suggest that weaker DNA binding of Rfa1 does not have detectable effect on the recombinational repair assays examined thus far, rather it has a profound effect in Srs2-mediated checkpoint downregulation. In-depth studies of rfa1-zm mutations in the context of various DSB repair steps will be interesting to pursue in the future.

With camptothecin, in the absence of site-specific damage, it is difficult to test these questions directly. (Perhaps there is a way to assess the total amount of RPA bound, but ongoing replication may obscure such a measurement). It should be possible to assess how CPT treatment in various genetic backgrounds affects the duration of Mec1/Rad53-dependent checkpoint arrest, but more than a FACS profile would be required. 

Quantitative measurement of RPA residence time on DNA in cells and the duration of Mec1/Rad53-dependent checkpoint arrest will be very informative but requires further technology development. Our current work provides a foundation for such quantitative assessment.

It is also notable that MMS treatment does not seem to yield similar results (Fig. S1). 

Figure S1 showed that srs2-∆PIM and srs2-3KR had weaker suppression of rfa1-zm2 growth on MMS plates than on CPT plates. The reasons for the less potent growth suppression in MMS condition compared with CPT condition are unclear, but multiple possibilities should be considered, given that MMS and CPT affect checkpoint responses differently and that RPA and Srs2 affect growth in multiple ways. For example, while CPT only activates the DNA damage checkpoint, MMS additionally induces DNA replication checkpoint (Menin et al., 2018, Redon et al., 2003). It is thus possible that the Srs2-RPA antagonism is more important for the DNA damage checkpoint than the DNA replication checkpoint. Further investigation of this and other possibilities will provide clues to the differential suppressive effects seen in this work. We will include this discussion in the revised text.

Reviewer #3:

The superfamily I 3'-5' DNA helicase Srs2 is well known for its role as an anti-recombinase, stripping Rad51 from ssDNA, as well as an anti-crossover factor, dissociating extended D-loops and favoring non-crossover outcome during recombination. In addition, Srs2 plays a key role in ribonucleotide excision repair. Besides DNA repair defects, srs2 mutants also show a reduced recovery after DNA damage that is related to its role in downregulating the DNA damage signaling or checkpoint response. Recent work from the Zhao laboratory (PMID: 33602817) identified a role of Srs2 in downregulating the DNA damage signaling response by removing RPA from ssDNA. This manuscript reports further mechanistic insights into the signaling downregulation function of Srs2. 

Using the genetic interaction with mutations in RPA1, mainly rfa1-zm2, the authors test a panel of mutations in Srs2 that affect CDK sites (srs2-7AV), potential Mec1 sites (srs2-2SA), known sumoylation sites (srs2-3KR), Rad51 binding (delta 875-902), PCNA interaction (delta 1159-1163), and SUMO interaction (srs2SIMmut). All mutants were generated by genomic replacement and the expression level of the mutant proteins was found to be unchanged. This alleviates some concern about the use of deletion mutants compared to point mutations. The double mutant analysis identified that PCNA interaction and SUMO sites were required for the Srs2 checkpoint dampening function, at least in the context of the rfa1-zm2 mutant. There was no effect of these mutants in a RFA1 wild-type background. This latter result is likely explained by the activity of the parallel pathway of checkpoint dampening mediated by Slx4, and genetic data with an Slx4 point mutation affecting Rtt107 interaction and checkpoint downregulation support this notion. Further analysis of Srs2 sumoylation showed that Srs2 sumoylation depended on PCNA interaction, suggesting sequential events of Srs2 recruitment by PCNA and subsequent sumoylation. Kinetic analysis showed that sumoylation peaks after maximal Mec1 induction by DNA damage (using the Top1 poison camptothecin (CPT)) and depended on Mec1. These data are consistent with a model that Mec1 hyperactivation is ultimately leading to signaling downregulation by Srs2 through Srs2 sumoylation. Mec1-S1964 phosphorylation, a marker for Mec1 hyperactivation and a site found to be needed for checkpoint downregulation after DSB induction did not appear to be involved in checkpoint downregulation after CPT damage. The data are in support of the model that Mec1 hyperactivation when targeted to RPA-covered ssDNA by its Ddc2 (human ATRIP) targeting factor, favors Srs2 sumoylation after Srs2 recruitment to PCNA to disrupt the RPA-Ddc2-Mec1 signaling complex. Presumably, this allows gap filling and disappearance of long-lived ssDNA as the initiator of checkpoint signaling, although the study does not extend to this step.

Strengths 

(1) The manuscript focuses on the novel function of Srs2 to downregulate the DNA damage signaling response and provide new mechanistic insights. 

(2) The conclusions that PCNA interaction and ensuing Srs2-sumoylation are involved in checkpoint downregulation are well supported by the data. 

We thank the reviewer for carefully reading our work and for his/her positive comments. 

Weaknesses 

(1) Additional mutants of interest could have been tested, such as the recently reported Pin mutant, srs2Y775A (PMID: 38065943), and the Rad51 interaction point mutant, srs2-F891A (PMID: 31142613). 

srs2-Y775A was shown to be proficient for stripping RPA from ssDNA and behaved like wild-type Srs2 in assays such as gene conversion and crossover control, and exhibited a genetic interaction profile as the wildtype allele. The authors suggest that the Y775 pin can contribute to unwinding secondary DNA structures. Collectively, these findings do not provide a strong rationale for srs2-Y775A being relevant for RPA removal from ssDNA. 

We have already included the data showing that a srs2 mutant lacking the Rad51 binding domain (srs2-∆Rad51BD, ∆875-902) did not affect rfa1-zm2 growth in CPT nor caused other defects in CPT on its own (Figure 2D). This data suggest that Rad51 binding is not relevant to the Srs2-RPA antagonism in CPT, a conclusion fully supported by data in our previous study (Dhingra et al., 2021). Collectively, these findings do not provide a strong rationale to test a point mutation within the Rad51BD region. 

(2) The use of deletion mutants for PCNA and RAD51 interaction is inferior to using specific point mutants, as done for the SUMO interaction and the sites for post-translational modifications. 

We agree with this view generally. However, this is less of a concern for the Rad51 binding site mutant (srs2∆Rad51BD), as it behaved as the wild-type allele in our assays. The srs2-∆PIM mutant (lacking 4 amino acids) has been examined for PCNA binding in vitro and in vivo in several studies (e.g. Kolesar et al., 2016, Kolesar et al., 2012); to our knowledge no unintended defect was reported. We thus believe that this allele is suitable for testing whether Srs2’s ability to bind PCNA is relevant to RPA regulation.

(3) Figure 4D and Figure 5A report data with standard deviations, which is unusual for n=2. Maybe the individual data points could be plotted with a color for each independent experiment to allow the reader to evaluate the reproducibility of the results. 

We will include individual data points as suggested and correct figure legend to indicate that three independent biological samples per genotype were examined in both panels.

References:

Dhingra N, Kuppa S, Wei L, Pokhrel N, Baburyan S, Meng X, Antony E and Zhao X (2021) The Srs2 helicase dampens DNA damage checkpoint by recycling RPA from chromatin Proc Natl Acad Sci U S A 118

Hammet A, Magill C, Heierhorst J and Jackson SP (2007) Rad9 BRCT domain interaction with phosphorylated H2AX regulates the G1 checkpoint in budding yeast EMBO Rep 8: 851-857

Kolesar P, Altmannova V, Silva S, Lisby M and Krejci L (2016) Pro-recombination Role of Srs2 Protein Requires SUMO (Small Ubiquitin-like Modifier) but Is Independent of PCNA (Proliferating Cell Nuclear Antigen) Interaction J Biol Chem 291: 7594-7607

Kolesar P, Sarangi P, Altmannova V, Zhao X and Krejci L (2012) Dual roles of the SUMO-interacting motif in the regulation of Srs2 sumoylation Nucleic Acids Res 40: 7831-7843

Koster DA, Palle K, Bot ES, Bjornsti MA and Dekker NH (2007) Antitumour drugs impede DNA uncoiling by topoisomerase I Nature

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Author response:

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

eLife assessment

The authors use point light displays to measure biological motion (BM) perception in children (mean = 9 years) with and without ADHD, and relate it to IQ, social responsiveness scale (SRS) scores and age. They report that children with ADHD were worse at all three BM tasks, but that those tasks loading more heavily on local processing relate to social interaction skills and those loading on global processing relate to age. There are still some elements of the results that are unclear, but nevertheless, the important and solid findings extend our limited knowledge of BM perception in ADHD, as well as biological motion processing mechanisms in general.

We thank the editors and reviewers for their valuable feedback and constructive comments. In the revised manuscript, we have incorporated all statistics for the models and also provided detailed analytical evidence about the distinct contributions of local and global BM processing. We hope these clarifications could enhance the robustness of our conclusions.

Public Reviews:

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.

We appreciate the your positive feedback very much.

Weaknesses:

The manuscript has improved in clarity and conceptual and methodological considerations in response to the last review. However, the reported results still provide incomplete support for the claims the authors make in the paper.

In relation to other reviewers' earlier comments, the model notation used is still not consistent and model results are reported incompletely, which make it difficult to gain a full picture of the data and how they support the authors' secondary claims. For instance, across the models in the supplementary materials, ß coefficients are only reported selectively which makes it difficult to assess the model as a whole. Furthermore, different terms (task 1, task 2 vs. BM-Local, BM-global) are used to refer to the same levels of a variable, and it is unclear which levels of a dummy variable correspond to which task, making it overall very difficult to comprehend the modelling procedure.

Thanks for pointing out these issues. In the revised version, we have unified the terminology by consistently referring to task types as BM-Local, BM-Global, BM-General. Additionally, we have provided clarification on the interpretation of dummy variables in relation to model construction. Furthermore, we corrected the model results and included all statistics in Table S1, S2, and S3. For more detailed information, please refer to the response to your Recommendations for the authors.

Reviewer #3 (Public Review):

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 valuable and solid findings are informative for understanding this complex condition, as well as biological motion processing mechanisms in general. However, the correlations present a pattern that needs further examination in future studies because many of the differences between correlations are not significant.

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.

Thanks for this positive assessment of our work.

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 this further. 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.

We apologize for not clarifying these points earlier. We did identify correlations between performance on all BM tasks and SRS scores. However, it is noteworthy that this finding is not unexpected, given the significant distinctions in SRS scores between TD and ADHD children, alongside their marked differences in all BM tasks. Correlation analyses involving data from both groups may reflect group differences. To elucidate the relationship between social ability impairment and diminished BM processing in children with ADHD, we conducted additional subgroup analyses and found correlations only in the BM-local task. To further support the specificity of this correlation, we compared the differences in coefficients. We revised our modelling procedure for testing differences between correlations in supplementary materials and presented all models statistics in Table S2, S3. Discrepancies in these coefficients, which exclude the influence of differences between groups, suggest that social factors specifically influence the performance of the BM-Local task in children with ADHD. We acknowledge that the analysis for differences between correlations is based on a relative small sample size and provided modest interpretation in discussion. Future studies will aim to increase the sample size to validate our findings.

Theoretical assumptions. The authors make some statements about local vs global biological motion processing that may have been made in previous studies, but would appear controversial and not definitive. E.g., that local BM processing does not improve with age and is uninfluenced by attention.

Thanks for your comment. To the best of our knowledge, there have been fewer developmental studies conducted on local BM processing compared to global BM processing. Our study is the first one to directly explore the relationship between local BM processing and age. Additionally, we used QbInattention to evaluate sustained attention function (considered as “top-down” attention) and examined its correlation with local BM processing. Some indirect evidence supported that the ability to process local BM cues remained stable and was unaffected by top-down attention. For example, local BM processing did not show a learning trend (Chang 2009) and was linked to the activation of subcortical regions (Hirai 2020). Research has demonstrated that local BM cues can convey information about walking direction without participants’ explicit attention or recognition (Chang 2009, Hirai 2011, Thompson 2007, Wang 2010), indicating the involvement of “bottom-up” processing (Hirai 2020, Troje 2023). Consistent with previous findings, we did not find significant correlation between local BM processing and age or QbInattention. We acknowledge that the statement such as “local BM processing does not improve with age and is uninfluenced by attention” should be approached with cautions. Therefore, we interpreted our results carefully:

“Once a living creature is detected, an agent (i.e., is it a human?) can be recognised by a coherent, articulated body structure that is perceptually organised based on its motions (i.e., local BM cues)71. This involves top-down processing and probably requires attention25,72, particularly in the presence of competing information26. Our findings are consistent with those of previous studies on the cortical processing of BM73, as we found that the severity of inattention in children with ADHD was negatively correlated with their performance in global BM processing, whereas this significant correlation was not found in local BM processing, which may involve bottom-up processing61,65 and might not need participants’ explicit attention21,23,74,75. However, further studies are needed to verify this hypothesis.” (lines 461-470)

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Supplementary materials: For all reported results, I suggest the authors use consistent model notation with complete reporting of all statistics in line with common conventions (ideally tables reporting beta values, error terms and confidence intervals for all model predictors, as well as R squared values). In particular the beta values for the reference category are needed to be able to fully interpret the beta values for the reported contrasts.

We appreciate the your suggestion. In the newly revised manuscript, we reported all statistics including beta values, error terms and confidence intervals for all model predictors, and R squared values. These detailed statistics can be found in Table S1, S2 and S3. We hope this additional information will offer readers a more comprehensive understanding of our study.

Please also address the following inconsistencies:

- At least when reporting the model results, the same term should be used when refering to task type (either task 1/2/3/ or local/global/general BM).

Thank the your for this feedback. We use the same term (BM-Local/Global/General) to refer to task type in the whole text.

- Second linear model in the Supplementary Materials: The authors state that the results suggest that the correlation between SRS and task 1 is greater than that between task 2 and SRS scores. First of all, to be able to support this claim the authors need to provide the coefficient for task 1 (which, if task 1 is the reference variable should be ß1). Second, as I currently understand the reported model results, the fact that ß4 (representing the difference in relationship to SRS scores between task 2 and task 1; the authors refer to ß3 here although I assume they mean ß4) is negative and shows a trend towards significance would actually mean the relationship between BM processing accuracy and SRS scores is more negative for task 2 relative to task 1 and not, as the authors state, that the correlation with SRS scores is greater for task 1. I realise this contradicts the individual r values and scatter plots and hope the authors can clarify the model results.

We thank you for pointing out these issues. For the second linear model (Model 4 in revised manuscript), we reported the coefficients for all predictors and model summaries including the coefficient for task 1 (ß1). In addition, we have made correction to the model results. The values of ß4 (representing the difference in relationship to SRS scores between BM-Global and BM-Local) and ß5 (representing the difference in relationship to SRS scores between BM-General and BM-Local) were positive and showed a trend towards significance, indicating that the correlations with SRS total score were more negative for BM-Local relative to BM-Global and BM-General:

“A general linear model was constructed (Table S2, Model 4): SRS = β0 + β1 * ACC + β2 * D1 + β3 * D2 + β4 * (ACC * D1) + β5 * (ACC * D2). If the effect of the interaction term (i.e., β4 or β5 ) is statistically significant, it indicates a difference in correlations with SRS total score between BM-Local and BM-Global (or BM-General). The results suggested trends where the correlations with SRS total score were more negative for BM-Local relative to BM-Global (standardized β4 \= 0.580 p = 0.074) and BM-General (standardized β5 = 0.550 p = 0.073).” (lines SI 36-42)

- Third linear model in the Supplementary Materials: In the dummy variable representing task, when local BM is the reference level, which task is represented by d1 and d2, respectively? If I understand the authors' procedure correctly, d1 should represent the difference between local and global BM and d2 the difference between local and general BM. If this is true, ß4 should code for the difference between local and global BM and not, as stated by the authors, for the difference between local and general BM. Also, what is d3?

Thank you for pointing out this issue. We corrected and clarified the results of third model (Model 5 in revised manuscript) in the revised version and pointed out what is represented by d1 (D1) and d2 (D2), respectively:

“We recoded task types into two dummy variables, D1 and D2, using BM-Local as a reference. The coefficient of D1 represents the difference in relationship to age between BM-Local and BM-Global, and the coefficient of D2 represents the difference in relationship to age between BM-Local and BM-General. The following model was created for each group (Table S3, Model 5-6): ACC = β0 + β1 * age + β2 * D1 + β3 * D2 + β4 * (age * D1) + β5 * (age * D2). If the effect of the interaction term (i.e., β4 or β5) is statistically significant, it indicates a difference in the effect of age on ACC between BM-Local and BM-Global (or BM-General). In the ADHD group, we observed a significant difference in the effect of age on ACC between BM-Local and BM-General (standardized β5 \= 0.462, p < 0.001) and marginally significant differences in the effect of age on ACC between BM-Local and BM-Global (standardized β4 \= 0.228, p = 0.073).” (lines SI 47-57)

Author response:

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

Reviewer 3:

Response to authors' revisions:

This reviewer is not convinced that the authors have done enough to satisfactorily address either of the major issues described in the original public review, above.

They're still not providing a quantification of Fig. 5D (originally 5C).

Their response regarding the expression pattern of Rh1 is particularly concerning, as it represents a misinterpretation of previously published data.

The gene encoding Rh1, ninaE, is expressed at such high levels in R1-6 PRs that any RNA-seq data (bulk or single-cell) generated from the optic lobes, no matter what cell-type, will display some ninaE transcripts that are present in the background, as they leak from R1-6 during dissociation steps. This phenomenon has been well described, for instance in Davis et al., 2020, eLife, and in fact led to the development of computational tools to abate such artifacts. In other words: no, rh1 is not expressed in glia, or any other neuron besides PRs for that matter. Therefore, I remain deeply suspicious about the functional relevance of the regulatory mechanisms described in this paper.

We thank the reviewer for her or his critical comments.

We quantified the cell-type differences in translation of the reporter with Tub-GAL4 and now show the results in Figure 5F. Consistent with other results, this analysis revealed that the glia-to-neuron ratio of the reporter protein expression is significantly lower when it contains the UTR sequences of rh1.  

We removed the mRNA counts (former Figure 5A and Figure 5 - figure supplement 1A), as we agree that these may well be contaminated by the very high rh1 expression in R1-6. We also amended the graph showing the ribosome distribution on the rh1 mRNA (Figure 5B) to better compare the translational efficiency (footprints normalized with mRNA, in a similar manner to Figure 3C). Now it clearly highlights the cell-type differences of footprint distributions; ribosomes are much more enriched on the CDS (being translated) in neurons, while the fraction of ribosomes on the 5ʹ leader (being stalled) is much higher in glia. We summarized this differential ribosome distribution in a new graph (now Figure 5C).  

We apologize for the misleading description of the reporter experiments. Despite the high level of mRNA expression in the R1-6, we chose the 5ʹ leader of rh1 for the translation reporter, as it contains clear uORFs and differential ribosome accumulation thereon (Figure 5B). This biased ribosome distribution and differential translation are the consistent features for many neuronal genes (Figure 3). We revised the text to clarify this point (Line 195-203).

In summary, we provide more rigorous analysis and extensive revision, which we hope clarified the concern.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript focuses on the role of the deubiquitinating enzyme UPS-50/USP8 in endosome maturation. The authors aimed to clarify how this enzyme drives the conversion of early endosomes into late endosomes. Overall, they did achieve their aims in shedding light on the precise mechanisms by which UPS-50/USP8 regulates endosome maturation. The results support their conclusions that UPS-50 acts by disassociating RABX-5 from early endosomes to deactivate RAB-5 and by recruiting SAND-1/Mon1 to activate RAB-7. This work is commendable and will have a significant impact on the field. The methods and data presented here will be useful to the community in advancing our understanding of endosome maturation and identifying potential therapeutic targets for diseases related to endosomal dysfunction. It is worth noting that further investigation is required to fully understand the complexities of endosome maturation. However, the findings presented in this manuscript provide a solid foundation for future studies.

We thank this reviewer for the instructive suggestions and encouragement.

Strengths:

The major strengths of this work lie in the well-designed experiments used to examine the effects of UPS-50 loss. The authors employed confocal imaging to obtain a picture of the aftermath of the USP-50 loss. Their findings indicated enlarged early endosomes and MVB-like structures in cells deficient in USP-50/USP8.

We thank this reviewer for the instructive suggestions and encouragement.

Weaknesses:

Specifically, there is a need for further investigation to accurately characterize the anomalous structures detected in the ups-50 mutant. Also, the correlation between the presence of these abnormal structures and ESCRT-0 is yet to be addressed, and the current working model needs to be revised to prevent any confusion between enlarged early endosomes and MVBs.

Excellent suggestions. The EM imaging indeed revealed an increase in enlarged cellular vesicles containing various contents in usp-50 mutants. However, the detailed molecular features of these vesicles remain unclear. Therefore, we plan to utilize ESCRT components for double staining with early or late endosome markers. This will enable us to accurately characterize the anomalous structures detected in the usp-50 mutants.

Reviewer #2 (Public Review):

Summary:

In this study, the authors study how the deubiquitinase USP8 regulates endosome maturation in C. elegans and mammalian cells. The authors have isolated USP8 mutant alleles in C. elegans and used multiple in vivo reporter lines to demonstrate the impact of USP8 loss-of-function on endosome morphology and maturation. They show that in USP8 mutant cells, the early endosomes and MVB-like structures are enlarged while the late endosomes and lysosomal compartments are reduced. They elucidate that USP8 interacts with Rabx5, a guanine nucleotide exchange factor (GEF) for Rab5, and show that USP8 likely targets specific lysine residue of Rabx5 to dissociate it from early endosomes. They also find that the localization of USP8 to early endosomes is disrupted in Rabx5 mutant cells. They observe that in both Rabx5 and USP8 mutant cells, the Rab7 GEF SAND-1 puncta which likely represents late endosomes are diminished, although Rabex5 is accumulated in USP8 mutant cells. The authors provide evidence that USP8 regulates endosomal maturation in a similar fashion in mammalian cells. Based on their observations they propose that USP8 dissociates Rabex5 from early endosomes and enhances the recruitment of SAND-1 to promote endosome maturation.

We thank this reviewer for the instructive suggestions and encouragement.

Strengths:

The major highlights of this study include the direct visualization of endosome dynamics in a living multi-cellular organism, C. elegans. The high-quality images provide clear in vivo evidence to support the main conclusions. The authors have generated valuable resources to study mechanisms involved in endosome dynamics regulation in both the worm and mammalian cells, which would benefit many members of the cell biology community. The work identifies a fascinating link between USP8 and the Rab5 guanine nucleotide exchange factor Rabx5, which expands the targets and modes of action of USP8. The findings make a solid contribution toward the understanding of how endosomal trafficking is controlled.

We thank this reviewer for the instructive suggestions and encouragement.

Weaknesses:

- The authors utilized multiple fluorescent protein reporters, including those generated by themselves, to label endosomal vesicles. Although these are routine and powerful tools for studying endosomal trafficking, these results cannot tell whether the endogenous proteins (Rab5, Rabex5, Rab7, etc.) are affected in the same fashion.

Good suggestion. Indeed, to test whether the endogenous proteins (Rab5, Rabex5, Rab7, etc.) are affected in the same fashion as fluorescent protein reporters, we supplemented our approach with the utilization of endogenous markers. These markers, including Rab5, RAB-5, Rabex5, RABX-5, and EEA1 for early endosomes, as well as RAB-7, Mon1a, and Mon1b for late endosomes, were instrumental in our investigations (refer to Figure 3, Figure 6, Sup Figure 4, Sup Figure 5, and Sup Figure 7). Our comprehensive analysis, employing various methodologies such as tissue-specific fused proteins, CRISPR/Cas9 knock-in, and antibody staining, consistently highlights the critical role of USP8 in early-to-late endosome conversion.

- The authors clearly demonstrated a link between USP8 and Rabx5, and they showed that cells deficient in both factors displayed similar defects in late endosomes/lysosomes. However, the authors didn't confirm whether and/or to which extent USP8 regulates endosome maturation through Rabx5. Additional genetic and molecular evidence might be required to better support their working model.

Excellent point. We plan to conduct additional genetic analyses, including the construction of double mutants between usp-50 and various rabex-5 mutations, to further elucidate the extent to which USP8 regulates endosome maturation via Rabex5.

Reviewer #3 (Public Review):

Summary:

The authors were trying to elucidate the role of USP8 in the endocytic pathway. Using C. elegans epithelial cells as a model, they observed that when USP8 function is lost, the cells have a decreased number and size in lysosomes. Since USP8 was already known to be a protein linked to ESCRT components, they looked into what role USP8 might play in connecting lysosomes and multivesicular bodies (MVB). They observed fewer ESCRT-associated vesicles but an increased number of "abnormal" enlarged vesicles when USP8 function was lost. At this specific point, it's not clear what the objective of the authors was. What would have been their hypothesis addressing whether the reduced lysosomal structures in USP8 (-) animals were linked to MVB formation? Then they observed that the abnormally enlarged vesicles, marked by the PI3P biosensor YFP-2xFYVE, are bigger but in the same number in USP8 (-) compared to wild-type animals, suggesting homotypic fusion. They confirmed this result by knocking down USP8 in a human cell line, and they observed enlarged vesicles marked by YFP-2xFYVE as well. At this point, there is quite an important issue. The use of YFP-2xFYVE to detect early endosomes requires the transfection of the cells, which has already been demonstrated to produce differences in the distribution, number, and size of PI3P-positive vesicles (doi.org/10.1080/15548627.2017.1341465). The enlarged vesicles marked by YFP-2xFYVE would not necessarily be due to the loss of UPS8. In any case, it appears relatively clear that USP8 localizes to early endosomes, and the authors claim that this localization is mediated by Rabex-5 (or Rabx-5). They finally propose that USP8 dissociates Rabx-5 from early endosomes facilitating endosome maturation.

Weaknesses:

The weaknesses of this study are, on one side, that the results are almost exclusively dependent on the overexpression of fusion proteins. While useful in the field, this strategy does not represent the optimal way to dissect a cell biology issue. On the other side, the way the authors construct the rationale for each approximation is somehow difficult to follow. Finally, the use of two models, C. elegans and a mammalian cell line, which would strengthen the observations, contributes to the difficulty in reading the manuscript.

The findings are useful but do not clearly support the idea that USP8 mediates Rab5-Rab7 exchange and endosome maturation, In contrast, they appear to be incomplete and open new questions regarding the complexity of this process and the precise role of USP8 within it.

We thank this reviewer for the insightful comments. Fluorescence-fused proteins serve as potent tools for visualizing subcellular organelles both in vivo and in live settings. Specifically, in epidermal cells of worms, the tissue-specific expression of these fused proteins is indispensable for studying organelle dynamics within living organisms. This approach is necessitated by the inherent limitations of endogenously tagged proteins, whose fluorescence signals are often weak and unsuitable for live imaging or genetic screening purposes. Acknowledging concerns raised by the reviewer regarding potential alterations in organelle morphology due to overexpression of certain fused proteins, we supplemented our approach with the utilization of endogenous markers. These markers, including Rab5, RAB-5, Rabex5, RABX-5, and EEA1 for early endosomes, as well as RAB-7, Mon1a, and Mon1b for late endosomes, were instrumental in our investigations (refer to Figure 3, Figure 6, Sup Figure 4, Sup Figure 5, and Sup Figure 7). Our comprehensive analysis, employing various methodologies such as tissue-specific fused proteins, CRISPR/Cas9 knock-in, and antibody staining, consistently highlights the critical role of USP8 in early-to-late endosome conversion. Specifically, we discovered that the recruitment of USP-50/USP8 to early endosomes is depending on Rabex5. However, instead of stabilizing Rabex5, the recruitment of USP-50/USP8 leads to its dissociation from endosomes, concomitantly facilitating the recruitment of the Rab7 GEF SAND-1/Mon1. In cells with loss-of-function mutations in usp-50/usp8, we observed enhanced RABX-5/Rabex5 signaling and mis-localization of SAND-1/Mon1 proteins from endosomes. Consequently, this disruption impairs endolysosomal trafficking, resulting in the accumulation of enlarged vesicles containing various intraluminal contents and rudimentary lysosomal structures.

Through an unbiased genetic screen, verified by cultured mammalian cell studies, we observed that loss-of-function mutations in usp-50/usp8 result in diminished lysosome/late endosomes. To elucidate the underlying mechanisms, we investigated the formation of multivesicular bodies (MVBs), a process tightly linked to USP8 function. Extensive electron microscopy (EM) analysis indicated that MVB-like structures are largely intact in usp-50 mutant cells, suggesting that USP8/USP-50 likely regulate lysosome formation through alternative pathways in addition to their roles in MVB formation and ESCRT component function. USP8 is known to regulate the endocytic trafficking and stability of numerous transmembrane proteins. Interestingly, loss-of-function mutations in usp8 often lead to the enlargement of early endosomes, yet the mechanisms underlying this phenomenon remain unclear. Given that lysosomes receive and degrade materials generated by endocytic pathways, we hypothesized that the abnormally enlarged MVB-like vesicular structures observed in usp-50 or usp8 mutant cells correspond to the enlarged vesicles coated by early endosome markers. Indeed, in the absence of usp8/usp-50, the endosomal Rab5 signal is enhanced, while early endosomes are significantly enlarged. Given that Rab5 guanine nucleotide exchange factor (GEF), Rabex5, is essential for Rab5 activation, we further investigated its dynamics. Additional analyses conducted in both worm hypodermal cells and cultured mammalian cells revealed an increase of endosomal Rabex5 in response to usp8/usp-50 loss-of-function. Live imaging studies further demonstrated active recruitment of USP8 to newly formed Rab5-positive vesicles, aligning spatiotemporally with Rabex5 regulation. Through systematic exploration of putative USP-50 binding partners on early endosomes, we identified its interaction with Rabex5. Comprehensive genetics and biochemistry experiments demonstrated that USP8 acts through K323 site de-ubiquitination to dissociate Rabex5 from early endosomes and promotes the recruitment of the Rab7 GEF SAND-1/Mon1. In summary, our study began with an unbiased genetic screen and subsequent examination of established theories, leading to the formulation of our own hypothesis. Through multifaceted approaches, we unveiled a novel function of USP8 in early-to-late endosome conversion.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This study makes an interesting finding: a polyunsaturated fatty acid, Lin-Glycine, increases the conductance of KCNQ1/KCNE1 channels by stabilizing a state of the selectivity filter that allows K+ conduction. The stabilization of a conducting state appears well supported by single-channel analysis, though some method details are missing. The linkage to PUFA action through the selectivity filter is supported by the disruption of PUFA effects by mutation of residues which change conformation in two KCNQ1 structures from the literature. Claims about differences in Lin-Glycine binding to these two structural conformations seem to lack clear support, thus the claim seems speculative that PUFAs increase Gmax by binding to a crevice in the pore domain. A potentially definitive functional experiment is conducted by single-channel recordings with selectivity filter domain mutation Y315F which ablates the Lin-Glycine effect on Gmax. However, this appears to be an n=1 experiment. Overall, the major claim of the abstract is supported: "... that the selectivity filter in KCNQ1 is normally unstable ... and that the PUFA-induced increase in Gmax is caused by a stabilization of the selectivity filter in an open-conductive state." However, the claim in the abstract that selectivity filter instability "explains the low open probability" seems too general.

We thank the reviewer for the comments, and we would like to address the main concern regarding the single channels. We now state the number of experiments used for the single channel analysis. We agree that the claim in the abstract seems too general and we now made it more specific to our findings.

Reviewer #2 (Public Review):

Golluscio et al. address one of the mechanisms of IKs (KCNQ1/KCNE1) channel upregulation by polyunsaturated fatty acids (PUFA). PUFA is known to upregulate KCNQ1 and KCNQ1/KCNE1 channels by two mechanisms: one shifts the voltage dependence to the negative direction, and the other increases the maximum conductance (Gmax). While the first mechanism is known to affect the voltage sensor equilibrium by charge effect, the second mechanism is less known. By applying the single-channel recordings and mutagenesis on the putative binding sites (most of them related to the selectivity filter), they concluded that the selectivity filter is stabilized to a conductive state by PUFA binding.

Strengths:

They mainly used single-channel recordings and directly assessed the behavior of the selectivity filter. The method is straightforward and convincing enough to support their claims.

Weaknesses:

The structural model they used is the KCNQ1 channel without KCNE1 because KCNQ1/KCNE1 channel complex is not available yet. As the binding site of PUFAs might overlap with KCNE1, it is not very clear how PUFA binds to the KCNQ1 channel in the presence of KCNE1.

Using other previous PUFA-related KCNQ1 mutants will strengthen their conclusions. For example, the Gmax of the K326E mutant is reduced by PUFA binding. Examining whether K326E shows reduced numbers of non-empty sweeps in the single-channel recordings will be a good addition.

We thank the reviewer for the public review. We would like to address the main weak points of the comments. As a structure of KCNQ1/KCNE1 in complex is not available yet, we used KCNQ1 alone. We believe that the PUFA and KCNE1 binding sites will not overlap as we previously presented data in agreement with the idea that KCNE1 rotates the VSD relative the PD (Wu et al., 2021). This would leave enough space for both PUFA and KCNE1, so that PUFA can bind to the crevice (K326 and D301) without competing with KCNE1.  We appreciate the suggestion of adding single-channel recordings of K326E mutant and we agree it would make a valuable addition to strengthen our conclusions. However, single channel recordings for KCNQ1 are very challenging and time consuming to obtain, so we would like to keep this in consideration for future studies.

Reviewer #3 (Public Review):

This manuscript reveals an important mechanism of KCNQ1/IKs channel gating such that the open state of the pore is unstable and undergoes intermittent closed and open conformations. PUFA enhances the maximum open probability of IKs by binding to a crevice adjacent to the pore and stabilizing the open conformation. This mechanism is supported by convincing single-channel recordings that show empty and open channel traces and the ratio of such traces is affected by PUFA. In addition, mutations of the pore residues alter PUFA effects, convincingly supporting that PUFA alters the interactions among these pore residues.

Strengths:

The data are of high quality and the description is clear.

Weaknesses:

Some comments about the presentation.

(1) The structural illustrations in this manuscript in general need to be more clarified.

(2) The manuscript heavily relies on the comparison between the S4-down and S4-up structures (Figures 3, 4, and 7) to illustrate the difference between the extracellular side of the pore and to lead to the hypothesis of open-state stability being affected by PUFA. This may mislead the readers to think that the closed conformation of the channel in the up-state is the same as that in the down-state.

We thank the reviewer for the public review, and we would like to address the comments about the presentation. We agree that the structural illustrations need to be more detailed, and we amended our previous illustrations. We have now included a new Figure 3 with a more detailed legend and a new Figure 4 that includes more information, such as the main chain of the whole selectivity filter and surrounding peptide.

We have now added some clarification regarding the structures of KCNQ1 with S4-down and S4-up to clarify that the closed conformation of the channel in the up-state is different from that in the down-state. We also emphasize this difference in the Discussion.

Recommendations for the authors:

Reviewer #1:

(1) Explain more thoroughly how the single-channel recordings were done:

- How was Lin-Glycine applied in these experiments? The patch configuration is unclear. Was Lin-Glycine added to the patch pipette? If not, why is Lin-Glycine expected to reach the proposed binding site in the outer leaflet? Were controls time-matched applications of vehicles with ethanol?

Data were collected using the cell attached patch configuration to minimize disruption to the patch and avoid rundown problems due to the loss of PIP2. Lin-Glycine was solubilized in DMSO and the desired concentration was added directly to the bath. We had no a priori reason to know if the PUFA would reach the proposed binding site but the consistency at which there was an increase in channel activity 5-10 minutes after addition to the bath convinced us that it was indeed reaching the binding site. This time frame fits with our prior experience with mefenamic acid effects on single channels (Wang et al 2020). The mefenamic acid binding site is external to the membrane so the drug must enter the cell and cross the patch membrane to affect channel activity. In addition, shown below is a previous recording from our lab, where nothing was added to the bath over a 55-minute time while recording consecutive files.  This shows the typical behavior of IKs, with activity tending to cluster with a few active sweeps in between many blank sweeps.  The behavior in this patch contrasts with that seen in the presence of Lin-glycine, where the clusters of activity spread over an increasing number of sweeps.

In addition, we have previously shown that 0.1% DMSO (concentration used in the present study) does not affect the GV of KCNQ1 but there is a non-significant decrease in tail current amplitudes of about 14% (Eldstrom et al., 2021). As such we do not think that the effects we see with Lin-Glycine, with an increase in activity can be explained by vehicle effects alone.

Author response image 1.

 

We added some more details in the section Material and Method.

- How well the replicates match the representative data in Figures 1, S1, and 6 is unclear (except for average current and Po in the last second of the traces from Figure 1). Are the results in Fig 6 n=1? 

We now show in a data supplement that 3 replicates were used to access the change in channel activity upon addition of Lin-glycine.

- Diary plots (as in Werry et al. 2013) and additional descriptions of the timeline of Lin-Glycine application and analyses could add credibility to interpretations. 

We added a Diary plot of for the First latency to open in Supplementary Figure S1.

- Amounts of plasmids and lipofectamine that were used in transfections are missing. 

We added the information in Material and Method section as follow:

“Single channel currents were recorded from transiently transfected mouse ltk- fibroblast cells (LM cells) using 1.5 mL Lipofectamine 2000 (Thermo Fisher Scientific). Cells were transfected with 1.5 mg of pcDNA3 containing a linked KCNE1-KCNQ1 construct 20, to ensure fully KCNE1-saturated complexes, in addition to a plasmid containing green fluorescent protein (GFP) to identify transfected cells”

- Inclusion/exclusion criteria for patches analyzed are missing. 

We added the information in Material and Method section as follow:

“Only patches that were largely free of endogenous currents and had few channels, such that there were several blank sweeps to average for use for leak subtraction, were analyzed.”

- Whether blinding, randomization, or pre-determined n values were employed is not mentioned. 

No blinding, randomization or pre-determined n values were employed.

- Analysis methods are sometimes unclear: How was Po calculated? Representative sweeps appear to have been leak and capacitance subtracted. How was that done? 

Po was estimated from all-point amplitude histogram as follow: Po = Sum (iN/(iestimateNtotal), where N is the number of points for a specific current i in the histogram, iestimate = 0.4 pA from the peak of the histogram, and Ntotal = 10,000 is the total number of points in the last second of the trace. p = 0.75 ± 0.12 (n = 8) and p = 0.87 ± 0.04 (n = 3) for Control and Lin-Glycine, respectively.

Leak and capacitance were subtracted with averaged empty sweeps.

(2) The change of cells used for whole cell vs single channel (oocytes vs mouse ltk- fibroblast cells) could be discussed. These cells likely have different lipids in their membranes. Is there any other evidence that PUFAs have the same effects on KCNE1-KCNQ1 in these cells? Does the V0.5 shift? 

A similar effect on Gmax, in both oocytes and mouse ltk-fibroblast cells, is shown in Figure 1 and 2. In Figure 2, the shift in latency suggests a shift in V0.5, suggesting the binding of PUFA to Site I.

(3) The manuscript associates selectivity filter changes with S4 being up or down. It would help to clarify whether there was a change in [K+] in the two KCNQ1 structures used for modeling, as Mandala and MacKinnon (2023) state: "We note that one interesting difference between the two up structures regards the occupancy of K+ ions in the selectivity filter (SI Appendix, Fig. S5 C and D). In the polarized sample, due to the low extravesicular concentration of K+, density is only visible at the first and third positions in the selectivity filter, while density is present at all four positions in the unpolarized sample. Similar differences were observed in our previous study on Eag (20) and are qualitatively consistent with crystal structures of KcsA solved under symmetrical high and low K+ concentrations (45)." 

Our studies states that there are some differences in the two structures with S4 in up-state and S4 in down-state and a reorganization of the pore. As for the change in [K+] occupancy in the two structures, we are not sure as our knowledge only come from what stated in Mandala and Mackinnon (2023). Mandala and MacKinnon did not discuss the selectivity filter in the down state structure in their paper and there are no K ions in any of their pdb files. So, we don’t know how many K+ ions there are in the down state.

(4) The manuscript states " PUFAs increase Gmax by binding to a crevice in the pore domain" and "we elucidated that Lin-Glycine binds to a crevice between K326 and D301", this seems speculative without any actual binding studies or concrete structural evidence. A quantitative structural modeling analysis of whether changes in the crevice change the theoretical binding of Lin-Glycine might provide a stronger basis for speculation. 

We toned down these statements in Results and Discussion to:

“Crevice residues affect PUFA ability to increase Gmax"

And

Discussion: “We tested the hypothesis that the effect of Lin-Glycine involved conformational changes in the selectivity filter following PUFA binding to two residues K326 and D301 at the pore domain. Those residues delimit a small crevice that seems to change in size in different structures with S4 up or S4 down (Figure 3, D-F).”

(5) The several figures detailing differences in selectivity filter conformation in the KCNQ1 structures are interesting and relevant in that they identify the movement of residues such as Y315 that, when mutated, ablate Lin-Glycine effect on Gmax. It would help to clarify whether T312 and I313 also move between the two selectivity filter conformations. 

From the morph of the selectivity filter in the two conformations, it is noticeable that the changes and residue movements involve only residues at the upper part of the selectivity filter (including Y315 and D317). T312 and I313, are in the lower part of the selectivity filter and do not seem to move or rotate from their position between the two conformations of the selectivity filter.

We now include a Supplementary Figures S3 and S4 that show the extent of movement of each residue in the pore region and a short description of this in the Results section.

(6) The claim in the abstract that selectivity filter instability "explains the low open probability" seems too general. Lin-Glycine seems to increase the likelihood of conduction by 2.5-fold, but it was not clear whether open probability ceases to be low or whether other mechanisms also keep Po low. 

We reword this sentence to “Our results suggest that the selectivity filter in KCNQ1 is normally unstable, contributing to the low open probability, and that the PUFA-induced increase in Gmax is caused by a stabilization of the selectivity filter in an open-conductive state..”

Reviewer #2:

(1) While all the electrophysiological recordings used KCNQ1/KCNE1 channels, all the structural models they used are KCNQ1 channels (without KCNE1). I know it is because the KCNQ1/KCNE1 complex structure is unavailable. However, according to their previous results, KCNQ1 alone is also upregulated by PUFAs. I am curious about what the single-channel recordings of KCNQ1 alone look like in the presence and absence of PUFAs. 

We would love to include single-channel recordings of KCNQ1, but they are extremely hard to measure due to the small size and flickering nature of the channel.

(2) As mentioned above, we do not have the KCNQ1/KCNE1 structure yet have the KCNQ1/KCNE3 structures (Sun and MacKinnon, Cell, 2020). According to the PDBs (6V00 or 6V01), the clevis (K326 and D301) looks covered by KCNE3. Is it true that PUFAs do not upregulate KCNQ1/KCNE3? If true, KCNE1 may not cover the clevis, so the binding mode should differ from the KCNQ1/KCNE3 structures. Please discuss the possible blocking of the clevis by KCNE proteins. 

We previously presented data that is consistent with that KCNE1 rotates the VSD towards the PD (Wu et al., 2021). This mechanism would leave room for PUFA and KCNE1, so that PUFA can bind to the crevice (K326 and D301). So we think that this rotation will prevent PUFA and KCNE1 from competing for the same space. As for KCNQ1/KCNE3 we currently do not have any evidence about a possible upregulation by PUFA.

(3) In the cryoEM structure with S4 resting (Figure 3F), the clevis looks too narrow for PUFA to bind. Is there any (either previous or current) evidence supporting that PUFA binding is state-dependent? 

Because PUFAs integrate first into the bilayer and then diffuse towards its binding site on the channel, it would be hard to test a state-dependence of the binding. In addition, once PUFAs are in the bilayer, the rate of binding/unbinding is quite fast (within the ns range according to our previous MD simulations), whereas opening/closing rate is very slow (100 ms-s). So, the combination of slow wash in/washout, fast binding/unbinding, and slow opening/closing would make it very difficult to test the state-dependence of the binding by using a fast perfusion or different voltage protocols.  

(4) In the previous report (Liin et al. Cell Reports, 2018), K326 is the most critical site for PUFA binding. Why the K326 mutants are not included in the current study? I also would like to see the single-channel recordings of the K326E mutant, which showed a smaller Gmax. Does the PUFA application reduce the probability of non-empty traces in this mutant? 

As Liin et al. reported, mutations of K326 reduce the ability of PUFA to increase the Gmax. In this work, we wanted to gain further biophysical information on the mechanism that leads to an increase in Gmax, considering the knowledge we had from work conducted in our lab previously. We therefore focused here on residues downstream of K326 that we think are important for inducing the conformational changes at the selectivity filter. We agree that single channel experiments on K326E would be very interesting but that has to be for a future study.

Minor points 

(1) Liin et al. used S209F (Po of 0.4) and I204F (Po of 0.04) mutants. Their single-channel recordings would be a good addition. 

We thank the reviewer for the suggestion. However, single channels analysis on S209F and I204F were previously shown (Eldstrom et al., 2010).

(2) I would like to see how the Site I mutations (R2Q/Q3R) affect (or do not affect) the single-channel recordings (open probability and latency). 

Thank you for the excellent suggestion. It would be interesting to assess the behavior of the channel when mutations occur at Site I. However, we think this information will not add any more detail to this study as we focus here our attention on the mechanism for Gmax increase. Single channels recordings are extremely hard to get, therefore we chose to include only mutations at Site II for this study.

(3) I would like the G-V curves for all the mutations at 0 and 20 uM of Lin-Glycine (Figure 3C and Figures 5A and B). 

We now added the G-V curves in Supplementary Figure S7.

(4) I assume all the PUFAs have a similar effect on the selectivity filter, but a few other examples of PUFAs would be nice to see. 

We anticipate that PUFAs and analogues with similar properties to Lin-Glycine would increasing the Gmax by a similar mechanism, because other PUFAs have been previously shown to increase the Gmax (Bohannon et al., 2020).

(5) Although the probabilities of non-empty sweeps are written in the manuscript, bar graph presentations would be a nice addition to Figures 2 and 6. 

We have added bar graphs of non-empty sweeps for Fig 2 and 6 in.

(6) Is there no statistical significance for D317E and T309S in Figure 5A? 

No statistical significance for D317E and T309S

(7) There is no reference to Figure 7 in the manuscript. 

A reference to Figure 7 has been added to the manuscript in the following paragraph.

“Taken together, our results suggest that the binding of PUFA to Site II increases Gmax by promoting a series of interactions that stabilize the channel pore in the conductive state. For instance, we speculate that in the conductive state, hydrogen bonds between W304-D317 and W305-Y315, which are likely absent in the non-conductive conformation of KCNQ1, are created and that PUFA binding to Site II favors the transition towards the conductive state of the channel (Figure 7)”

Reviewer #3:

(1) Clarify the structural figures. Figures 3 D, E, and F - explain what the colors indicate. 

A more detailed description of Figure 3 has been added to the legend.

“D, E and F) Structure of crevice between S5 and S6 in KCNQ1 with S4 up (D and E) and S4 down (F). Residues that surround the crevice from S6 shown in blue (K326, T327, S330, V334) and from S5 in red (D301, A300, L303, F270). Remaining KCNQ1 residues shown in purple…, linoleic acid (LIN: gold color)”

Fig 4. Only side chains of the residues are shown, making it hard to relate the figure to the familiar K channel selectivity filter. The main chain of the entire selectivity should be shown to orient readers to the familiar view of the K channel selectivity filter. In addition, the structures shown are only part of the selectivity filter, it should be specified which part of the selectivity filter is shown. These will also help the discussion at the bottom of page 10 and subsequent text. 

We now provide a new Figure 4 with more details such as the main chain of the whole selectivity filter and surrounding peptide.

(2) Cautions should be stated clearly when the structural comparison between the S4-up and S4-down is made that the structure of the pore when it is closed with S4-up may differ from the structure of the pore with S4-down. 

We now state in addition “Clearly, there will be other differences in the pore domain between structures with activated and resting VSDs, for example the state of the activation gate.”

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Wu et al. explores the role of the histone reader protein SntB in Aspergillus flavus, claiming it to be a key regulator of development and aflatoxin biosynthesis. While the study incorporates various techniques, including gene deletion, ChIP-seq, and RNA-seq, several concerns and omissions in the paper raise questions about the validity and completeness of the presented findings.

(1) Omissions of Prior Work:

The authors fail to acknowledge and integrate prior research by Pfannenstiel et al. (2018) on the sntB gene in A. flavus, which covered phenotypic changes, RNA-seq data, and histone modifications. This omission raises concerns about the transparency and completeness of the current study.

The absence of reference to studies by Karahoda et al. (2022, 2023) revealing SntB's involvement in the KERS complex in A. flavus and A. nidulans is a major oversight. This raises questions about the specificity of SntB's regulatory functions, as it may be part of a larger complex. The authors should clarify why these studies were omitted and how they ensure that SntB alone, and not the entire KERS complex, is responsible for the observed effects.

We very appreciate reviewer’s professional question. As reviewer mentioned, Pfannenstiel et al. (2018) reported the functions of sntB gene covered secondary metabolism, development and global histone modifications in A. flavus and we also cited this paper (please see reference 20). In their study, the functions of sntB gene were analyzed by both Δ_sntB_ and overexpression sntB genetic mutants. SntB deletion impaired several developmental processes, such as sclerotia formation and heterokaryon compatibility, secondary metabolite synthesis, and the ability to colonize host seeds, which were consistent with our results (Figure 1 and 2). Unlike, a complementation strain was constructed in our study which further clarified and confirmed the function of sntB gene. What’s more, our main purpose is to find the downstream regulatory mechanism of SNTB, which was reported to be a transcription factor, not only as an important epigenetic reader. Please see lane 452-457 and lane 486-500.

For the function of KERS complex in A. nidulans (Karahoda et al., 2022), we had cited the papers, please see reference 29. For the report about the function of KERS complex in A. flavus (Karahoda et al., 2023), this paper was published recently. We are sorry for the omissions of this work. In our revised manuscript, we have cited this paper and compared with our work. Please see lane 97-98 and reference 30. Based solely on our experiments, we cannot confirm whether it is acting alone or in conjunction with others, what we can confirm is that SntB plays a key role in the process. And we will conduct related research in the future.

(2) Transparency and Accessibility of Data:

The lack of accessibility and visualization tools for ChIP-seq and RNA-seq data poses a challenge for independent verification and in-depth analysis. The authors should address this issue by providing more accessible data or explaining the limitations of data availability. A critical component missing from the paper is a detailed presentation of ChIP-seq data, specifically demonstrating SntB binding patterns on key promoters. This omission weakens the link between SntB and the mentioned regulatory genes. The authors should include these crucial data visualizations to strengthen their claims.

To review GEO accession GSE247683, you can go to https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE247683, and enter the token “ipilouscnruprsl” into the box. And after our paper being published, the data will be released. For the SntB binding patterns on key promoters, we have added in the Figure 4, please see Figure 4D, 4E, 5F, 5G, and table S9.

(3) SntB Binding Sites and Consensus Sequence:

The study mentions several genes upregulated in the sntB mutant without demonstrating SntB binding sites on their promoters. A detailed analysis of SntB binding maps is necessary to establish a direct link between SntB and these regulatory genes.

Thanks for your suggestion. We have added the binding maps of SntB, please see Figure 5F, 5G; lane 362-364.

(4) Mechanistic Insight into Peroxisome Biogenesis:

If SntB indeed regulates peroxisome biogenesis, the absence of markers for peroxisomes and the localization of peroxisomes in the sntB mutant vs. WT strains is a significant gap. Providing evidence for peroxisome regulation is crucial for understanding the proposed mechanism and validating the study's claims.

Thanks for your suggestion. Catalase is ubiquitously present in aerobic organisms and plays a crucial role in mitigating oxidative stress through the scavenging of reactive oxygen species (ROS). So, we detected the ROS level in sntB mutant and WT strain, as well as ∆catC strain (Figure 6H).

In summary, while the manuscript presents intriguing findings regarding SntB's role in A. flavus, the omissions of prior work, lack of transparency in data accessibility, and insufficient mechanistic insights call for revisions and additional experimental evidence to strengthen the validity and impact of the study. Addressing these concerns will enhance the manuscript's contribution to the field.

Thanks. We have revised our manuscript depending on the valuable comments provided above.

Additionally, the way the English language is used could be improved.

Thanks. We have asked a native English-writing assistant to proof read the paper and revised the grammar errors and typos and improve the readability and quality of the manuscript.

Reviewer #2 (Public Review):

Summary:

This work is of great significance in revealing the regulatory mechanisms of pathogenic fungi in toxin production, pathogenicity, and in its prevention and pollution control. Overall, this is generally an excellent manuscript.

Strengths:

The data in this manuscript is robust and the experiments conducted are appropriate.

Weaknesses:

(1) The authors found that SntB played key roles in the oxidative stress response of A. flavus by ChIP-seq and RNA sequencing. To confirm the role of SntB in oxidative stress, the authors have to better measure the ROS levels in the ΔsntB and WT strains, besides the ΔcatC strain.

Thanks for your suggestion. We have supplemented the relevant experiments and the results were shown in Figure 6G and lane 185-192 and 395-398.

(2) Why did the authors only study the function of catC among the 7 genes related to an oxidative response listed in Table S14?

The function of some genes in Table S15 (Table S14 in old version of our manuscript) had been studied, such as cat1 [1]. In this study, we just choose catC for further validation, which was the most up-regulated gene in Δ_sntB_ strain. The others may also have important roles in SntB triggered antioxidant pathways to regulate development and aflatoxin biosynthesis in A. flavus. We will focus on this in the following work.

(1) Zhu Z., Yang M., Bai Y., Ge F., Wang S. Antioxidant-related catalase CTA1 regulates development, aflatoxin biosynthesis, and virulence in pathogenic fungus Aspergillus flavus [J]. Environ Microbiol, 2020, 22(7): 2792-2810.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Line 52: Change "shad light" to "shed light"

Thanks. We have revised. Please see lane 50.

Line 62: Change "has" to "have" to match the plural noun "aflatoxins."

Original: "Aflatoxins produced by A. flavus has strong toxicity..."

Suggested: "Aflatoxins produced by A. flavus have strong toxicity..."

Thanks. We have revised it. Please see lane 62.

Line 79: Consider rephrasing for clarity.

Original: "...which may result in the modulation of the expression of genes involved in toxin production [15-17]."

Thanks. We have revised. Please see lane 77-80.

Line 105: Add a comma after "host strain."

Original: "A. flavus Δku70 ΔpyrG was used as a host strain for genetic manipulations."

Suggested: "A. flavus Δku70 ΔpyrG was used as a host strain, for genetic manipulations."

Thanks. We have revised it. Please see lane 107.

Line 113, Table 1: Remove the extra "r" in "from" in the Source column.

Original: "Kindly presented form Prof. Chang[1]"

Suggested: "Kindly presented from Prof. Chang[1]"

Thanks. We have revised it. Please see Table 1.

Line 140: Typo - Change "reaches" to "reach."

Original: "when silkworm larva reaches about 1 g in weight."

Suggested: "when silkworm larvae reach about 1 g in weight."

Thanks. We have revised it. Please see lane 141.

Line 158: Typo - Change "pervious" to "previous."

Original: "Data processing was according pervious study [39]."

Suggested: "Data processing was according to a previous study [39]."

Thanks. We have revised it. Please see lane 150.

Line 138 The animal invasion assay using silkworms was conducted according to a previous study.

Change "according" to "conducted according to" for clarity.

Thanks. We have revised it. Please see lane 139.

Line 148 Was carried out by APPLIED PROTEIN TECHNOLOGY, Shanghai (www. aptbiotech.com).

Change "TECHNOLOY" corrected to "TECHNOLOGY."

Thanks. We have revised it. Please see lane 149.

Line 148 Data processing was conducted according to a previous study [39].

Change "according to" to "conducted according to" for clarity.

Thanks. We have revised it. Please see lane 139.

Line 429 Schizzosaccharomyces pombe, Correct the spelling to "Schizosaccharomyces pombe [55]."

Thanks. We have revised it. Please see lane 448.

Reviewer #2 (Recommendations For The Authors):

(1) The resolution of the words written in Figures 3 and 4 is not clear (or high) enough.

Thanks. We have revised them. Please see Figures 3 and 4.

(2) Which kind of protein marker (protein ladder) was used in Figure 4A, you should mark out the size of the related protein.

Thanks. We have revised. Please see Figure 4A and lane 332-333.

(3) Latin names do not necessarily need to be written in full when they are not the first time used in the text.

Thanks. We have revised them throughout the manuscript.

(4) The complementary strain of sntB was labeled as sntB-C in Figure 2B, while in other figures was Com-sntB. You should correct all related problems.

Thanks. We have revised it. Please see Figure 2B.

(5) What is the meaning of "1" in Table 1?

Thanks. The meaning of "1" in Table 1 was a citation. We have revised. Please see Table 1.

Author response:

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

eLife assessment

The manuscript constitutes an important contribution to antimalarial drug discovery, employing diverse systems biology methodologies; with a focus on an improved M1 metalloprotease inhibitor, the study provides convincing evidence of the utility of chemoproteomics in elucidating the preferential targeting of PfA-M1. Additionally, metabolomic analysis effectively documents specific alterations in the final steps of hemoglobin breakdown. These findings underscore the potential of the developed methodology, not only in understanding PfA-M1 targeting but also in its broader applicability to diverse malarial proteins or pathways. Revisions are needed to further enhance overall clarity and detail the scope of these implications.

We thank the editor and reviewers for recognising the contribution our work makes to understanding the selective targeting of aminopeptidase inhibitors in malaria parasites and the wider impact this multi-omic strategy can have for anti-parasitic drug discovery efforts. The reviewers have provided constructive feedback and raised important points that we have taken on-board to improve our manuscript. In particular, we have revised aspects of the text and figures to enhance clarity, performed additional analysis on the other possible MIPS2673 interacting proteins and more comprehensively analysed the effect of MIPS2673 on parasite morphology. NB: Specific responses to comments in the public reviews are provided within responses to the specific recommendations to authors.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The article "Chemoproteomics validates selective targeting of Plasmodium M1 alanyl aminopeptidase as a cross-species strategy to treat malaria" presents a series of biochemical methods based on proteomics and metabolomics, as a means to:

(1) validate the specific targeting of biologically active molecules (MIPS2673) towards a defined (unique) protein target within a parasite and (2) to explore whether by quantifying the perturbations generated at the level of the parasite metabolome, it is possible to extrapolate which metabolic pathway has been disrupted by using this biologically active molecule and whether this may further confirm selective targeting in parasites of the expected (or in-vitro targeted) enzyme (here PfA-1).

The inhibitor used in this work by the authors (MIPS2673) is to my knowledge a novel one, although belonging to a chemical series previously explored by the authors, which recently enabled them to discover a specific PfA-M17 inhibitor, MIPS2571 (Edgard et al., 2022, ref 11 of this current work). Indeed, inhibitors specifically targeting either PfA-M1 or PfA-M17 (and not both, as currently done in the past) are scarce today, and highly needed to functionally characterize these two zinc-aminopeptidases. MIPS2673, blocks the development of erythrocytic stages of Plasmodium falciparum with an EC50 of 324 nM, blocks the parasite development at the young trophozoite stage at 5x EC50 (but at ring stages at 10xEC50, figure 1E), and inhibits the enzymatic activity of PfA-M1 (and its ortholog Pv-M1) but not of the related malarial metallo-aminopeptidases (M17 and M18 families) nor the human metalloenzymes from closely related enzymatic families, supporting its selective targeting of PfA-M1 (and Pv-M1).

All experiments are carried out in vitro (e.g. biochemical studies such as enzymology, proteomics, metabolomics) and on cultured parasites (erythrocyte stages of Plasmodium falciparum and several gametocytes stages obtained in vitro); there are no in vivo manipulations. The work related to Plasmodium vivax, which justifies the "cross-species" indication in the title of the article, is restricted to using a recombinant form of the M1-family aminopeptidase in enzymatic assays. The rest of the work concerns only Plasmodium falciparum. While I found globally that this work is original and brings new data and above all proposes chemical validation approaches that could be used for other target validations under similar limiting conditions (impossibility of KO of the gene), I have some specific questions to address to the authors.

Strengths and weaknesses:

- The chemoproteomic approach, that explores the ability of MIPS2673 to more significantly "protect" the putative target (PfA-M1) against thermal degradation or enzymatic attack (by proteinase K), to document its selective targeting towards PfA-M1 (the inhibitor, once associated with its target, is expected to stabilize its structure or prevent the action of end proteases), uses several concentrations of MIPS2673 and provides convincing results. My main criticism is that these tests are carried out with parasite extracts enriched in 30-38 hours old forms, and restricted to the fraction of soluble proteins isolated from these parasitic forms, which still limits the scope of the analysis. It is clear that this methodological approach is a choice that can be argued both biologically (PfA-M1 is well expressed in these stages of the parasite development) and biochemically (it is difficult to do proteomic analyses on insoluble proteins) but I regret that the authors do not discuss these limitations further, notably, I would have expected (from Figure 1E) some targets to be also present at ring stages.

- The metabolomic approach, by documenting the ability of MIPS2673 to selectively increase the number of non-hydrolyzed dipeptides in treated versus untreated parasites is another argument in favor of the selective targeting of PfA-M1 by MIPS2673, in particular by its broad-spectrum aminopeptidase action preferentially targeting peptides resulting from the degradation of hemoglobin by the parasite. The relative contribution of peptides derived from host hemoglobin versus other parasite proteins is, however, little discussed.

The work as a whole remains highly interesting, both for the specific topic of PfA-M1's role in parasite biology and for the method, applicable to other malarial drug contexts.

Reviewer #2 (Public Review):

In this manuscript, the authors first developed a new small molecular inhibitor that could target specifically the M1 metalloproteases of both important malaria parasite species Plasmodium falciparum and P. vivax. This was done by a chemical modification of a previously developed molecule that targets PfM1 as well as PfM17 and possibly other Plasmodial metalloproteases. After the successful chemical synthesis, the authors showed that the derived inhibitor, named MIPS2673, has a strong antiparasitic activity with IC50 342 nM and it is highly specific for M1. With this in mind, the authors first carried out two large-scale proteomics to confirm the MIPS2673 interaction with PfM1 in the context of the total P. falciparum protein lysate. This was done first by using thermal shift profiling and subsequently limited proteolysis. While the first demonstrated overall interaction, the latter (limited proteolysis) could map more specifically the site of MIPS2673-PfM1 interaction, presumably the active site. Subsequent metabolomics analysis showed that MIPS2673 cytotoxic inhibitory effect leads to the accumulation of short peptides many of which originate from hemoglobin. Based on that the authors argue that the MIPS2673 mode of action (MOA) involves inhibition of hemoglobin digestion that in turn inhibits the parasite growth and development.

Reviewer #3 (Public Review):

This is a manuscript that attempts to validate Plasmodium M1 alanyl aminopeptidase as a target for antimalarial drug development. The authors provide evidence that MIPS2673 inhibits recombinant enzymes from both Pf and Pv and is selective over other proteases. There is in vitro antimalarial activity. Chemoproteomic experiments demonstrate selective targeting of the PfA-M1 protease.

This is a continuation of previous work focused on designing inhibitors for aminopeptidases by a subset of these authors. Medicinal chemistry explorations resulted in the synthesis of MIPS2673 which has improved properties including potent inhibition of PfA-M1 and PvA-M1 with selectivity over a closed related peptidase. The compound also demonstrated selectivity over several human aminopeptidases and was not toxic to HEK293 cells at 40 uM. The activity against P. falciparum blood-stage parasites was about 300 nM.

Thermal stability studies confirmed that PfA-M1 was a binding target, however, there were other proteins consistently identified in the thermal stability studies. This raises the question as to their potential role as additional targets of this inhibitor. The authors dismiss these because they are not metalloproteases, but further analysis is warranted. This is particularly important as the authors were not able to generate mutants using in vitro evolution of resistance strategies. This often indicates that the inhibitor has more than one target.

The next set of experiments focused on a limited proteolysis approach. Again several proteins were identified as interacting with MIPS2673 including metalloproteases. The authors go on to analyze the LiP-MS data to identify the peptide from PfA-M1 which putatively interacts with MIPS2673. The authors are clearly focused on PfA-M1 as the target, but a further analysis of the other proteins identified by this method would be warranted and would provide evidence to either support or refute the authors' conclusions.

The final set of experiments was an untargeted metabolomics analysis. They identified 97 peptides as significantly dysregulated after MIPS2673 treatment of infected cells and most of these peptides were derived from one of the hemoglobin chains. The accumulation of peptides was consistent with a block in hemoglobin digestion. This experiment does reveal a potential functional confirmation, but questions remain as to specificity.

Overall, this is an interesting series of experiments that have identified a putative inhibitor of PfA-M1 and PvA-M1. The work would be significantly strengthened by structure-aided analysis. It is unclear why putative binding sites cannot be analyzed via specific mutagenesis of the recombinant enzyme.

In the thermal stability and LiP -MS analysis, other proteins were consistently identified in addition to PfA-M1 and yet no additional analysis was undertaken to explore these as potential targets.

The metabolomics experiments were potentially interesting, but without significant additional work including different lengths of treatment and different stages of the parasite, the conclusions drawn are overstated. Many treatments disrupt hemoglobin digestion - either directly or indirectly and from the data presented here it is premature to conclude that treatment with MIPS2673 directly inhibits hemoglobin digestion.

Finally, the potency of this compound on parasites grown in vitro is 300 nM - this would need improvements in potency and demonstration of in vivo efficacy in the SCID mouse model to consider this a candidate for a drug.

Summary:

Overall, this is an interesting series of experiments that have identified a putative inhibitor of the Plasmodium M1 alanyl aminopeptidases, PfA-M1 and PvA-M1.

Strengths:

The main strengths include the synthesis of MIPS2673 which is selectively active against the enzymes and in whole-cell assay.

Weaknesses:

The weaknesses include the lack of additional analysis of additional targets identified in the chemoproteomic approaches.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Question 1. Line 737 (and elsewhere). Why are Plasmodium vivax orthologs of PfA-M1 and PfA-M17 called Pv-M1 and Pv-M17 and not PvA-M1 and PvA-M17, where A stands for Aminopeptidase? I would recommend changing the names if possible, although the mention of Pv-M1 and Pv-M17 is now current in the literature (which is kind of regrettable). See also Supplemental Table S1 where PfA-M1 is named Pf-M1.

Supplemental Table S1 was updated to PfA-M1. Nomenclature for the Plasmodium vivax aminopeptidase orthologs was amended to PvA-M1 and PvA-M17 as suggested by the reviewer.

Question 2. Figure 1. Observation of parasite culture slide smears in Figure 1E strongly suggests that an important target of MIPS2673 appears to be expressed at the ring stage or very young trophozoites, whereas the authors, in their proteomic and metabolomic analyses, performed studies focused on late trophozoites stages (30-38h post-invasion). This difference in the targeting of Plasmodium stages puzzles me and deserves some explanations from the authors, and is related to my question 3.

As the reviewer indicates, ring-stage parasite growth appears to be affected at high concentrations (5x and 10x EC50) of MIPS2673. Under these conditions, parasite growth appears to stall during late rings/early trophs at ~16-22 h post invasion when haemoglobin digestion is increasing and when one presumes PfA-M1 (the primary target of MIPS2673) is increasing in both expression and activity (see references 26 and 28 of this manuscript). Thus, whilst it is unsurprising that MIPS2673 has some activity against ring-stage parasites, we focused on the trophozoite stage for our proteomics studies as we showed this to be the stage most susceptible to MIPS2673 (Fig. 1D) and reasoned that we would most likely identify the primary MIPS2673 target, and other interacting proteins, from a complex biological mixture at this stage. The same reasoning underpinned our decision to perform metabolomics on drug-treated trophozoites, as we reasoned we would see a greater functional effect on this stage. Furthermore, performing these experiments on trophozoites rather than rings minimises the interference from the host red blood cell. While we cannot rule out additional targets in rings, repeating all experiments during this parasite stage is beyond the scope of this study.

Question 3. Figure 2. Although Figure 2 is insightful and somehow self-explanatory, I think it misses two specific pieces of information. First, it is indicated in line 618 (M&M) that parasite material for thermal stability and limited proteolysis studies correspond to synchronized parasites (30-38h post-invasion) but this information is not given in Figure 2. In addition, if I fully understand the experimental protocol of obtaining parasite extracts, they strictly correspond to the soluble protein fraction of the erythrocytic stages of plasmodium at the late trophozoite stage, and not to all parasitic proteins as the scheme of Figure 2 might suggest. I would appreciate it very much if these two points (parasite stages and soluble proteins) were clearly indicated in the scheme as indeed, not the whole parasite blood stage proteome is investigated in the study but just a part of it (~47%, as the authors indeed indicate line 406). Please, edit also the legend of the figure accordingly.

This is correct, the soluble protein fraction from synchronised trophozoites was used in our proteomics studies. These details have been included in an updated Figure 2 and in the corresponding figure legend.

Question 4. Thermal stabilization. Figure 3B. Could the authors explain how they calculated or measured "absolute" protein abundances, and how this refers to a number of parasites in initial assays as this is not clear to me. Notably, abundance for PfA-M1 is much higher than for PF3D7_0604300, which are interesting "absolute" values.

Protein abundance was calculated using the mean peptide quantity of the stripped peptide sequence, with only precursors passing the Q-value threshold (0.01) considered for relative quantification. Within independent experiments, normalisation was based on total protein amount (determined by the BCA assay) rather than the initial number of parasites.

PfA-M1 is known to be a highly abundant protein and PF3D7_0604300 (as well as the other protein hits identified by thermal stability proteomics) are likely less abundant. It is noted that abundance is also dependent on ionisation efficiency and trypsin digestion efficiency. Therefore, we avoid comparing absolute abundances across proteins and use relative differences across conditions instead.

NB: the word “absolute” in the text (“absolute fold-change”) refers to the absolute value of the fold-change (i.e. positive or negative), and not to absolute quantification of proteins. The preceding text in each case clarifies that these are based on “relative peptide abundance”.

Question 5. Figure 5A. How do the authors explain peptides whose abundances are decreasing instead of increasing? Figure 5C. Could the authors provide digital cues (aa numbers or positions) on the ribbon representation of the PfA-M1 sequence? It is difficult to correlate the position of the 3D domains with respect to the primary structure of the protein. Also, the "yellow" supposed to show the "drug ligand" is really not very visible.

LiP-MS is based on the principle that ligand binding alters the local proteolytic susceptibility of a protein to a non-specific protease (in this case proteinase K, PK). In this sense, in LiP-MS we are not looking at variations in the stability of whole proteins (as is the case with thermal stability proteomics, where proteins detected with significantly higher abundance in treated relative to control samples reflects thermal stabilisation of the target due to ligand binding), but differences in peptide patterns between treated and control samples that reflect a change in the ability of PK to cleave the target. Thus, in the bound state, the ligand prevents proteolysis with PK. This results in decreased abundance of peptides with non-tryptic ends (as PK cannot access the region around where the ligand is bound) and increased abundance of the corresponding fully tryptic peptide, when compared to the free target. This concept is demonstrated in Fig. 4A and is explained in the text (lines 279-282) and Fig. 4 figure legend.

To aid visualisation, we have not added amino acid positions on the PfA-M1 sequence in Fig. 5, but have provided amino acid positions for all peptides in Supplementary File 3. We have also changed the colour of the ligand in Fig. 5C to blue and increased transparency of the binding and centre of mass neighbourhoods.

Question 6. Gametocyte assays. Line 824 states that several compounds were used as positive controls for anti-gametocyte activity (chloroquine, artesunate, pyronaridine, pyrimethamine, dihydroartemisinin, and methylene blue) and line 821 states that the biological effects are measured against puromycin. This is not very clear to me, could the authors comment on this?

This wording has been clarified in the methods to reflect that 5 µM puromycin was used as the positive control to calculate percent viability, whereas the other antimalarials were run in parallel as reference compounds with known anti-gametocyte activity (line 862).

Question 7. Metabolomics. Metabolomic assays were done on parasites at 28h pi, incubated for 1h with 3x EC50 of MIPS2673. You mention applying the drug on 2x10E8 infected red blood cells (line 838) but you do not explain how you isolate these infected red blood cells from non-infected red blood cells. Could you please specify this?

Metabolomics studies were performed such that cultures at 2% haematocrit and 6% trophozoite-stage parasitaemia (representing 2 x 108 cells in total, rather than 2 x 108 infected cells) were treated with compound or vehicle and after 1 h metabolites were extracted. This methodological detail has been clarified in the methods (line 875).

Question 8. Figure 3B. Does this diagram come from the experimental 3D structure created by the authors (8SLO) or from molecular modeling? Please specify in the legend (line 1305).

The diagram showing the binding mode of MIPS2673 bound to PfA-M1 comes from the experimentally determined 3D structure (PDB ID: 8SLO). This has now been stated in the figure legend. Note that the structural diagram refers to Fig. 1B (not Fig. 3B as indicated by the reviewer). The experimentally determined PfA-M1 structure with MIPS2673 bound (PDB ID: 8SLO) was also used to map LiP peptides and estimate the MIPS2673 binding site in Fig. 5, which is also now reflected in the appropriate section of the text (line 308) and Fig. 5 legend.

Question 9. Line 745. Why not indicate µm concentration for this H-Leu-NHMec substrate while it is indicated for the other substrates mentioned in the rest of the paragraph (H-Ala-NHMec, 20 μM, etc..). Also in this section (Enzyme assays) the pH at which the various enzymatic assays were done is missing.

All enzyme assays were performed at pH 8.0. The concentration of H-Leu-NHMec varied depending on the enzyme assayed, as follows: 20 µM for PfA-M1, 40 µM for PvA-M1 and 100 µM for ERAP1 and ERAP2. This information is now clearly stated in the methods section (lines 782 and 787) and as a footnote for Supplemental Table S1.

Question 10. Line 830, please define FBS.

Fetal bovine serum (FBS) has been added where appropriate (line 867).

Question 11. The authors mention in the title the targeting of several plasmodium species, but the only experimental study on the Plasmodium vivax species concerns the use of the recombinant enzyme Pv-M1. Authors also mention "multi-stage targets", but ultimately only look at erythrocyte stages and three different gametocyte stages.

We have now removed the words “cross-species” and “multi-stage” from the manuscript title and abstract so as not to overstate these findings. We have also added the word “potential” in the manuscript text to clarify that selective M1 inhibition could offer a potential multistage and cross species strategy for malaria.

Question 12. Supplemental Table S1. I would suggest replacing "Percent inhibition by MIPS2673 of PfA-M1 and Pv-M1 aminopeptidases compared to selected human M1 homologues" with "Percent inhibition by MIPS2673 of PfA-M1 and Pv-M1 aminopeptidase activities compared to selected human M1 homologues".

Done.

Question 13. Supplemental Table S3. Here you indicate IC50 while in text and Figure 1 you quote EC50. Why this difference?

This has now been changed to EC50 in Supplemental Table S3.

Reviewer #2 (Recommendations For The Authors):

Amendments that I would recommend in order to improve the presentation include all four parts of the study:

(1) In vitro antiparasitic activity of MIPS2673.

The authors showed that MIPS2673 inhibits parasite growth with IC50 of 324nM measured by a standard drug sensitivity assay, Fig 1C. This is all well and good, but it would be helpful to include at least one if not more other compounds such as antimalaria drugs and/or their earlier inhibitors (e.g. inhibitor 1) for comparisons. This is typically done to show that the assay in this manuscript is fully compatible with previous studies. It will also give a better view of how the selective inhibition of PfM1 kills the parasite, specifically.

Alongside MIPS2673, we also analysed the potency of the known antimalarial artesunate, which was found to have an EC50 of 4 nM. This value agrees with the expected potency of artesunate and indicates our MIPS2673 value of 324 nM is indeed compatible with previous studies. We have now reported the artesunate EC50 value for reference (lines 197-198 and Fig. S1).

Next, the authors proceeded to investigate the stage-specific effect of MIPS2673 but this time doing a survival assay instead of proper IC50 estimations (Figure 1. I wonder why? Drug survival assays have typically very limited information content and measuring proper IC50 in stage-specific wash-off assays would be much more informative.

We performed single concentration stage specificity assays to determine the parasite asexual stage at which MIPS2673 is most active. This involved washing off the compound after a 24 h exposure in rings or trophozoites and determining parasite viability in the next asexual lifecycle. While a full dose response curve would allow generation of an EC50 value against the respective parasite stages, this information is unlikely to change the interpretation that MIPS2673 is more active against trophozoites stages than against rings.

Finally, in Figure 1E, the authors present the fact that the MIPS2673 arrests the parasite development. This is done by presenting a single (presumably representative) cell per time point. This is in my view highly insufficient. I recommend this figure be supplemented by parasite stage counts or other more comprehensive data representation. Also, the authors mention that while there is a growth arrest, hemoglobin is still being made. From the cell images, I can not see anything that supports this statement.

We thank the reviewer for this constructive comment and they are correct in their assessment that these are representative parasite images at the respective time points. To address the reviewers concerns we have now provided cell counts from each treatment condition (Fig. 1E) at selected time points, which shows parasite stalling at the ring to trophozoite transition under drug treatment. On reflection, we agree that it is difficult to determine the presence of haemozoin from our images and have removed this statement.

(2) Protein thermal shift profiling. In the next step, the authors proceed to carry out cellular thermal shift profiling to show that PfM1 indeed interacts with MIPS2673, this time in the context of the total protein lysates from P. falciparum. This section of the study is in my view quite solid and indeed it is nice to see that the inhibitor causes a thermal shift of PfM1 which further supports what was already expected: interaction.

I have no problem with this study in terms of the technical outcome but I would urge the authors to tone down the interpretation of these results in two ways.

Four other proteins were found to be shifted by the inhibitor which also indicates interactions. Calling it simply "off-target" interactions might not represent the truth. The authors should explore and in some way comment that interactions with these proteins could contribute to the MIPS2673 MOA. I do not suggest conducting any more studies but simply acknowledge this situation. Identifying more than one target is indeed very common in CETSA studies and it would be helpful to acknowledge this here as well.

We agree that identifying binding proteins in addition to the “expected” target is commonplace, and is indeed one of the benefits of this unbiased and proteome-wide approach. In the results and discussion, we have now amended our language to refer to these additional hits as MIPS2673-interacting proteins. In our original manuscript we dedicate a paragraph in the discussion to these additional interacting proteins and the likelihood of them being targets that contribute to antimalarial activity. Of these four additional interacting proteins, only the putative AP2 domain transcription factor (PF3D7_1239200) is predicted to be essential for blood stage growth and is therefore the only protein from this additional four that would likely contribute to antimalarial activity. These points are explicitly stated in the discussion (lines 530-550). Notably, all of the other interacting proteins identified in our thermal stability dataset were detected in our LiP-MS experiment but were not identified as interacting proteins by this method. The remaining three proteins were two non-essential P. falciparum proteins with unknown functions (PF3D7_1026000 and PF3D7_0604300) that are poorly described in the literature and a human protein (RAB39A). Further analysis of these other thermal stability proteomics hits in our LiP-MS dataset (see responses to Reviewer #3) identified none or only 1 significant LiP peptide from these proteins across our LiP-MS datasets, indicating they are likely to be false positive hits. Caveats around identifying protein targets by different deconvolution methods are also now addressed (lines 545-550).

At some point, the author argues that causing shifts of only four/five proteins including PfM1 shows that MIPS2673 does not interact with other (off) targets. Here one must be careful to present the lack of shifts in the CETSA as proof of no interaction. There are many reasons why thermal shifts are not observed including the physical properties of the individual proteins, detection limit etc. Again I suggest adjusting these statements accordingly.

We thank the reviewer for raising this important point and have now included additional discussion around this comment (lines 545-550).

Finally, I am not convinced that Figure 2 presents nothing more than the overall experimental scheme with not much new information. Many of such schemes were published previously in the original publication of thermal profiling. I would suggest omitting it from the main text and shifting it into supplementary methods etc.

We agree that similar schemes have been published previously, especially for thermal proteome profiling, and acknowledge the reviewer’s suggestion of moving this figure to the supplemental material. However, we have kept Fig. 2 in the main text as this scheme also incorporates a LiP-MS workflow for malaria drug target deconvolution (the first to do so) and also to satisfy the additional details requested for this figure by Reviewer #1 (question 3).

(3) Identification of MIPS2673 target proteins using LiP-MS. In the next step, the authors carried out the limited proteolysis analysis with the rationale that protein peptides that are near the inhibitor binding site will exhibit higher resilience to proteolysis. The authors did a very good job of showing this for PfM1-MISP2673 interaction. This part is very impressive from a technological perspective, and I congratulate the authors on such achievement. I imagine these types of studies require very precise optimizations and performance.

Here, however, I struggle with the meaning of this experiment for the overall flow of the manuscript. It seems that the binding pocket of MIPS2673 is less known since the inhibitor was designed for it. In fact, the authors mentioned that the crystal structure of PfM1 is available. From this perspective, the LiP-MS study represents more of a technical proof of concept for future drug target analysis but has limited contribution to the already quite well-established PfM1-MISP2673 interaction. Perhaps this could be presented in this way in the text.

We thank the reviewer for this comment and they are correct that we solved the crystal structure of PfA-M1 bound to MIPS2673. We wish to highlight that the primary reason for performing the LiP-MS study was as an independent and complementary target deconvolution method to narrow down the shortlist of targets identified with thermal stability proteomics, and validate with high confidence that PfA-M1 is indeed the primary target of MIPS2673 in parasites. The use of a complementary approach based on a different biophysical principle (proteolytic susceptibility vs thermal stability) would also allow us to identify MIPS2673 interacting proteins that may not be detectable by thermal stability proteomics, for example targets that do not alter their thermal stability upon ligand binding. The text in the results and discussion has been amended to clarify these points (lines 266-268 and 545-550).

Furthermore, we agree that correctly predicting the MIPS2673 binding site on PfA-M1 using our LiP-MS peptide data is a technical proof of concept. Indeed, we wished to highlight the potential utility of LiP-MS for identifying both the protein targets of drugs and predicting their binding site, which is not possible with many other target deconvolution approaches. This point has been updated in the text (lines 303-304, 459-461).

(4) Metabolomic profiling of MIPS2673 inhibition showed a massive accumulation of short peptides which clearly indicates that this inhibitor blocks some proteolytic activity of short peptides, presumably products of upstream proteolytic activities. Here the authors argue, that because many of these detected short (di-/tri-) peptides could be mapped on the hemoglobin protein sequence, this must be their origin. Although this might be the case the author could not exclude the fact that at least some of these come from other sources (e.g. Plasmodium proteins). It would be quite helpful to comment on such a possibility as well. In particular, it was mentioned that the main subcellular localization of PfM1 is in the cytoplasm while most if not all hemoglobin digestion occurs in the digestive vacuole...?

Indeed, we agree that Pf_A-M1 is likely processing both Hb and non-Hb peptides and do not definitively conclude that all dysregulated peptides must be derived from haemoglobin. A subset of dysregulated peptides cannot be mapped to haemoglobin and must have an alternative source such as other host proteins or turnover of parasite proteins. We have amended the discussion to better reflect these possible alternate peptide sources (480-482). Although the peptides detected in the metabolomics study (2-5 amino acids) are too short to be definitively assigned to any specific parasite or RBC protein, it is important to note that our analysis strongly indicates that the majority, but not all, of dysregulated peptides are more likely to originate from haemoglobin than other human or parasite proteins. This is based on sequence mapping, which was aided by acquiring MS/MS data for a subset of dysregulated peptides from which we derive accurate sequences (as opposed to residue composition inferred from total peptide mass) to more directly link dysregulated peptides to haemoglobin. We further quantified the sequence similarity of dysregulated peptides to all detectable proteins in the _P. falciparum infected erythrocyte proteome (~4700 proteins), showing that these peptides are statistically more similar to haemoglobin than other host or parasite proteins.

The apparent disconnect between PfA-M1 localisation (cytosol) and the predominant site of haemoglobin digestion (digestive vacuole, DV) is explained by the fact that peptides originating from digestion of haemoglobin in the DV are required to be transported into the cytoplasm for further cleavage by peptidases, including PfA-M1. This point has now been clarified in the discussion (lines 473-474).

Reviewer #3 (Recommendations For The Authors):

(1) Thermal stability studies confirmed that PfA-M1 was a binding target, however, there were other proteins consistently identified in the thermal stability studies. This raises the question as to their potential role as additional targets of this inhibitor. The authors dismiss these because they are not metalloproteases, but further analysis is warranted. This is particularly important as the authors were not able to generate mutants using in vitro evolution of resistance strategies. This often indicates that the inhibitor has more than one target.

We thank the reviewer for this comment. The possibility of other targets contributing to MIPS2673 activity was also raised by Reviewer #2 (question 2) and is addressed above. Further to our response to Reviewer #2, we agree that the inability to generate resistant parasites in vitro could indicate that inhibition of multiple essential parasite proteins (including PfA-M1) contribute to MIPS2673 activity and do not rule out this possibility. It may also indicate the target has a very high barrier for resistance and is unable to tolerate resistance causing mutations as they are deleterious to function. Indeed, previous attempts to mutate PfA-M1 (references 12 and 50), and our own attempts to generate MIPS2673 resistant parasites in vitro (unpublished), were unsuccessful. It is important to note that of the hits reproducibly identified using thermal stability proteomics, only PfA-M1 and a putative AP2 domain transcription factor (PF3D7_1239200) are predicted to be essential for blood stage growth. We have explicitly stated that PF3D7_1239200 could also contribute to activity (line 533 and 537).

As we identified multiple hits with thermal stability proteomics we employed the complementary LiP-MS method to further investigate the target landscape of MIPS2673. PfA-M1 was the only protein reproducibly identified as the target through this approach. Importantly, the five proteins identified as hits by thermal stability proteomics were also detected in our LiP-MS datasets, but only PfA-M1 was identified as a target by both target deconvolution methods, strongly indicating it is the primary target of MIPS2673 in parasites. An important caveat is that we profiled the soluble proteome (we did not include detergents necessary for extracting membrane proteins as they may interfere with these stability assays) and other factors (e.g. the biophysical properties of the protein) will impact on whether ligand induced stabilisation events are detected. We have added additional text in the discussion around the above points (lines 545-550).

While we do not definitively rule out other MIPS2673 interacting proteins existing in parasites (that possibly also contribute to activity), our metabolomics studies indicated no functional impact by MIPS2673 outside of elevated levels of short peptides. This is indicative of aminopeptidase inhibition and the profile of peptide accumulation was distinct from a known PfA-M17 inhibitor, and other antimalarials, further pointing to selective inhibition of the PfA-M1 enzyme by MIPS2673 being responsible for antimalarial activity.

(2) The next set of experiments focused on a limited proteolysis approach. Again several proteins were identified as interacting with MIPS2673 including metalloproteases. The authors go on to analyze the LiP-MS data to identify the peptide from PfA-M1 which putatively interacts with MIPS2673. The authors are clearly focused on PfA-M1 as the target, but a further analysis of the other proteins identified by this method would be warranted and would provide evidence to either support or refute the authors' conclusions.

As PfA-M1 was the only protein reproducibly identified as an interacting protein across both LiP-MS experiments (and by thermal stability proteomics) we focused our analysis on this protein. However, we agree that further analysis of the other putative interacting proteins would be valuable. Additional analysis was performed  (see new figure S4) on the other interacting proteins identified by thermal stability proteomics and the other interacting proteins identified in LiP-MS experiment one, as no other proteins (apart from PfA-M1) were identified as hits in the second LiP-MS experiment (lines 314-318, 495-505, 740-762 and Fig. S4). Using the common peptides detected across both LiP-MS experiments we mapped significant LiP peptides to the structures of the other putative MIPS2673-interacting proteins, where a structure was available and significant LiP-MS peptides were detected, and measured the minimum distance to expected binding sites. It is noted that when using the same criteria for a significant LiP peptide that we used for our PfA-M1 analysis, only one significant LiP peptide is identified from these other putative interacting proteins (YSPSFMSFK from PfADA). Therefore, we used a less stringent criteria for defining significant LiP peptides for these other proteins (see methods and Fig. S4 legend) in order to identify significant LiP peptides to map to structures. This analysis showed that, with the exception of PfA-M17, significant LiP-MS peptides for these other proteins are not significantly closer to binding sites than all other detected peptides, supporting our assertion that these other proteins are likely to be false positives or not functionally relevant MIPS2673 interacting proteins. Although significant peptides from PfA-M17 were closer to the binding site, our thermal stability and metabolomics data, combined with our previous work on the PfA-M17 enzyme, argue against this being a functionally relevant target (see lines 362-374 and 486-529 for a more detailed discussion). Another possible explanation for this result is that peptide substrates accumulating due to primary inhibition of PfA-M1 interact with PfA-M17, leading to structural changes around the enzyme active site that are detected by LiP-MS.

(3) The final set of experiments was an untargeted metabolomics analysis. They identified 97 peptides as significantly dysregulated after MIPS2673 treatment of infected cells and most of these peptides were derived from one of the hemoglobin chains. The accumulation of peptides was consistent with a block in hemoglobin digestion. This experiment does reveal a potential functional confirmation, but questions remain as to specificity.

As indicated, the accumulation of short peptides identified by metabolomics suggests MIPS2673 perturbs aminopeptidase function. Many of these peptides (but not all) likely map to haemoglobin and are more haemoglobin-like than other proteins in the infected red blood cell proteome. An effect on a subset of non-haemoglobin peptides is also apparent and we have added this to our discussion (also refer to our response to question 4 from Reviewer #2). A direct comparison to our previous metabolomics analysis of a specific PfA-M17 inhibitor (MIPS2571, reference 11) revealed MIPS2673 induces a unique metabolomic profile. The extent of peptide accumulation differed and a subset of short basic peptides (containing Lys or Arg) were elevated only by MIPS2673, consistent with the broad substrate preference of PfA-M1. Importantly, the metabolomics profile induced by MIPS2673 is the opposite of many other antimalarials, which cause depletion of haemoglobin peptides. Taken together, the profile of short peptide accumulation induced by MIPS2673 is consistent with specific inhibition of PfA-M1.

(4) Overall, this is an interesting series of experiments that have identified a putative inhibitor of PfA-M1 and PvA-M1. The work would be significantly strengthened by structure-aided analysis. It is unclear why putative binding sites cannot be analyzed via specific mutagenesis of the recombinant enzyme.

Contrary to this comment we solved the crystal structure of PfA-M1 bound to MIPS2673, determining its binding mechanism to the enzyme. This was further supported through proteomics-based structural analysis by LiP-MS. Undertaking site specific mutagenesis would be interesting to further probe the binding dynamics of MIPS2673 to the M1 protein. However, we believe it is beyond the scope of this study and would not change our conclusion that MIPS2673 binds to PfA-M1, which we have shown using multiple unbiased proteomics-based methods, enzyme assays and X-ray crystallography.

(5) In the thermal stability and LiP -MS analysis, other proteins were consistently identified in addition to PfA-M1 and yet no additional analysis was undertaken to explore these as potential targets.

As addressed in our previous responses, across independent thermal stability proteomics experiments we consistently identified 5 interacting proteins, including the expected target PfA-M1. In contrast, only PfA-M1 was reproducible across independent LiP-MS experiments. While several plausible putative targets (including aminopeptidases and metalloproteins) were identified in one of our LiP-MS experiment, they appear to be false discoveries and not responsible for the antiparasitic activity of MIPS2673, as peptide-level stabilisation was not consistent across independent LiP-MS experiments, and an interaction is refuted by our thermal stability, metabolomics and recombinant enzyme inhibition data. We have now performed further analysis of these other putative interacting proteins, which also argues against them being likely interacting proteins (see also response to question 2). We have also added to our existing discussion on possible MIPS2673 targets and the likelihood of these proteins contributing to antimalarial activity (lines 486-550).

(6) The metabolomics experiments were potentially interesting, but without significant additional work including different lengths of treatment and different stages of the parasite, the conclusions drawn are overstated. Many treatments disrupt hemoglobin digestion - either directly or indirectly and from the data presented here it is premature to conclude that treatment with MIPS2673 directly inhibits hemoglobin digestion.

Our metabolomics studies were performed using typical experimental conditions for investigating the antimalarial mechanisms of compounds by metabolomics (see references 11, 39, 40 and 55-57). We used a short 1 h incubation at 3x EC50 allowing us to profile the primary parasite pathways affected by MIPS2673 and avoid a nonspecific death phenotype associated with longer incubations. As addressed in our response to Reviewer #1 (question 2) we focused on trophozoite infected red blood cells as this is the stage most susceptible to MIPS2673 and when one presumes the greatest functional impact would be seen. It is possible that an expanded kinetic metabolomics analysis may reveal secondary mechanisms involved in MIPS2673 activity and we have now acknowledged this in the manuscript (lines 515-516). However, even though secondary mechanisms may become apparent at longer incubations it also becomes difficult to uncouple drug specific responses from nonspecific death effects. We believe any additional information provided by an expanded metabolomics analysis is unlikely to outweigh the significant extra financial cost associated with this type of experiment.

It is correct that many antimalarial compounds appear to disrupt haemoglobin digestion when analysed by metabolomics. However, as indicated in our manuscript (lines 369-373) and previous responses, the profile of elevated haemoglobin peptides induced by MIPS2673 is substantially different to the profile caused by other antimalarials. For example, artemisinins and mefloquine cause haemoglobin peptide depletion (references 55-57) and chloroquine results in increased levels of a different subset of non-haemoglobin peptides (see Creek et al. 2016). While there is some overlap in profile with a selective M17 inhibitor (our previous work, reference 11), the level of enrichment of these peptides is different and MIPS2673 also induces accumulation of a distinct set of basic peptides consistent with the substrate preference of the PfA-M1 enzyme. As we show that MIPS2673 does not inhibit other parasite aminopeptidases, a likely explanation for the profile overlap is that the build-up of substrates that cannot be processed by PfA-M1 leads to secondary dysregulation of other aminopeptidases. Our analyses (sequence mapping, MS/MS analysis and sequence similarities to all infected red blood cell proteins) strongly indicate that the majority of elevated peptides (but not all) originate from haemoglobin. Combined with our proteomics and recombinant enzyme data indicating direct engagement of PfA-M1, and with previous literature indicating the enzyme functions to cleave amino acids from haemoglobin-derived peptides, our data indicates MIPS2673 likely directly perturbs the haemoglobin digestion pathway through PfA-M1 inhibition.

(7) Finally, the potency of this compound on parasites grown in vitro is 300 nM - this would need improvements in potency and demonstration of in vivo efficacy in the SCID mouse model to consider this a candidate for a drug.

We do not propose MIPS2673 as an antimalarial candidate. The experiments presented here were centred on target validation rather than identification of an antimalarial lead, which may be the focus of future studies. To avoid this confusion, we have amended the manuscript title and language throughout to clarify this point.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Khan et. al., investigated the functional redundancy of the non-canonical L-cysteine synthases of M. tuberculosis, CysM and CysK2, focussing on their role in mitigating the effects of host-derived stress. They found that while deletion mutants of the two synthases (Rv∆cysM, Rv∆cysK2) have similar transcriptomes under standard conditions, their transcriptional response to oxidative stress is distinct. The impact of deleting the synthases also differentially affected the pools of L-cysteinederived metabolites. They show that the mutants (Rv∆cysM, Rv∆cysK2) have impaired survival in peritoneal macrophages and in a mouse model of infection. Importantly, they show that the survival of the mutants increases when the host is defective in producing reactive oxygen and nitrogen species, linking the phenotype to a defect in combating host-derived stress. Finally, they show that compounds inhibiting L-cysteine synthases reduce the intracellular survival of M.

tuberculosis.

Strengths:

(1) The distinct transcriptome of the Rv∆cysM and Rv∆cysK2 mutants in the presence of oxidative stress provides solid evidence that these mutants are distinct in their response to oxidative stress, and suggests that they are not functionally redundant.

(2) The use of macrophages from phox-/- and INF-/- mice and an iNOS inhibitor for the intracellular survival assays provides solid evidence that the survival defect seen for the Rv∆cysM and Rv∆cysK2 mutants is related to their reduced ability to combat host-derive oxidative and nitrosative stress. This is further supported by the infection studies in phox-/- and INF-/- mice.

Weaknesses:

(1) There are several previous studies looking at the transcriptional response of M. tuberculosis to host-derived stress, however, the authors do not discuss initial RNA-seq data in the context of these studies. Furthermore, while several of the genes in sulfur assimilation and L-cysteine biosynthetic pathway genes are upregulated by more than one stress condition, the data does not support the statement that it is the "most commonly upregulated pathway in Mtb exposed to multiple host-like stresses".

We have made changes in the manuscript in line with reviewer’s suggestion.  

“Thus RNA-Seq data suggest that genes involved in sulfur assimilation and L-cysteine biosynthetic pathway are upregulated during various host-like stresses in Mtb (Figure S2). Given the importance of sulphur metabolism genes in in vivo survival of Mtb [1, 2], it is not surprising that these genes are dynamically regulated by diverse environment cues. Microarray studies have shown upregulation of genes encoding sulphate transporter upon exposure to hydrogen peroxide and nutrient starvation [3-7] Similarly, ATP sulfurlyase and APS kinase is induced during macrophage infection and by nutrient depletion. Induction of these genes that coordinate first few steps of sulphur assimilation pathway indicate that probable increase in biosynthesis of sulphate containing metabolites that may be crucial against host inflicted stresses. Furthermore, genes involved in synthesis of reduced sulphur moieties (cysH, sirA and cysM) are also induced by hydrogen peroxide and nutrient starvation. Sulfur metabolism has been postulated to be important in transition to latency. This hypothesis is based on transcriptional upregulation of cysD, cysNC, cysK2, and cysM upon exposure to hypoxia. Multiple transcriptional profiling studies have reported upregulation of moeZ, mec, cysO and cysM genes when cells were subjected to oxidative and hypoxic stress [1, 6-11] further suggesting an increase in the biosynthesis of reduced metabolites such as cysteine and methionine and sulfur containing cell wall glycolipids upon exposure to oxidative stress [12]. We have modified the sentence to “significantly upregulated pathway in Mtb exposed to multiple host-like stresses”

(2) For the quantification of the metabolites, it isn't clear how the abundance was calculated (e.g., were standards for each metabolite used? How was abundance normalised between samples?), and this information should be included to strengthen the data.

Thanks for picking up this. We have extended our description of metabolomics methods. It now reads: “Due to the tendency of M. tuberculosis to form clamps, which significantly skews any cell number estimation we normalized samples to protein/peptide concentration using the BCA assay kit (Thermo). Therefore, our LC-MS data is expressed as ion counts/mg protein or ratios of that for the same metabolite. This is a standard way to express ion abundance data as it was done previously [13, 14].

Furthermore, labelling with L-methionine was performed to determine the rate of synthesis of the L-cysteine-derived metabolites. L-cysteine is produced from L-methionine via the transsulfuration pathway, which is independent of CysM and CysK2. It is therefore difficult to interpret this experiment, as the impact of deleting CysM and CysK2 on the transsulfuration pathway is likely indirect.

The reviewer may have misunderstood the experiment and the results presented. Labelling was not performed with L-methionine. We use 34S derived from SO42-, to monitor reductive assimilation of sulfur and its transit from S2- until L-methionine, passing through cysteine. We specified in material and methods that we have used sodium sulfate-34S (Merck 718882), as our label source of sulfur. This method was first employed in M. tuberculosis by the Bertozzi group to identify sulfolipids in mycobacteria. Therefore, we are not measuring transsulfuration, but instead direct synthesis of L-methionine via cysteine, and consequently we are indeed assessing the importance of cysK2 and cysM in this process. We have now added to the results section (page 9) that we employed (Na34SO4) for labeling, to make sure other readers will not think we are measuring transulfuration.

(3) The ability of L-cysteine to rescue the survival defect of the Rv∆cysM and Rv∆cysK2 mutants in macrophages is interpreted as exogenous L-cysteine being able to compensate for reduced intracellular levels. However, there is no evidence that L-cysteine is being taken up by the mutants and an alternate explanation is that L-cysteine functions as an antioxidant within cells i.e., it reduces intracellular ROS.

The concentration of L-cysteine used for peritoneal macrophage survival rescue experiments was titrated to have no minimum survival advantage in case of wild-type Rv. Thus, at the given concentration, we believe that the contribution of cysteine in reducing intracellular ROS within cells does not have a major role since there is no significant difference in the survival of wild-type Rv strain. Had cysteine reduced intracellular ROS, we would expect increased bacterial survival of Rv due to diminished oxidative stress. 

Furthermore, L-cysteine addition also mitigates CHP induced survival defect in vitro [15] and nullifies observed effect of Cysteine inhibitors in vitro [16] suggesting that cysteine or cystine can be transported into Mtb. This has also been previously shown in case of AosR mutant strain [15], CysH [2] and over 70% uptake of exogenously added [35S] cysteine to a growing culture of Mtb [17].

The authors sought to investigate the functional redundancy of the non-canonical L-cysteine synthases CysM and CysK2. While their distinct transcriptional response to oxidative stress suggests distinct physiological roles, the study did not explore these differences and therefore provides only preliminary insight into the underlying reasons for this observation. In the context of drug development, this work suggests that while L-cysteine synthase inhibitors do not have high potency for killing intracellular M. tuberculosis, they have the potential to decrease the pathogen's survival in the presence of host-derive stress.

Reviewer #2 (Public Review):

Summary:

The paper examines the role L-cysteine metabolism plays in the biology of Mycobacterium tuberculosis. The authors have preliminary data showing that Mycobacterium tuberculosis has two unique pathways to synthesize cysteine. The data showing new compounds that act synergistically with INH is very interesting.

Strengths:

RNAseq data is interesting and important.

Weaknesses:

The paper would be strengthened if the authors were to add further detail to their genetic manipulations.

The authors provide evidence that they have successfully made a cysK2 mutant by recombineering. This data looks promising, but I do not see evidence for the cysM deletion. It is also important to state what sort of complementation was done (multicopy plasmid, integration proficient vector, or repair of the deletion). Since these mutants are the basis for most of the additional studies, these details are essential. It is important to include complementation in mouse studies as unexpected loss of PDIM could have occurred.

The details of CysM knockout generation have been previously published ([15]; Appendix Figure S4), and complementation strain details are provided in the methods section.  

Reviewer #3 (Public Review):

In this work, the authors conduct transcriptional profiling experiments with Mtb under various different stress conditions (oxidative, nitrosative, low pH, starvation, and SDS). The Mtb transcriptional responses to these stress conditions are not particularly new, having been reported extensively in the literature over the past ~20 years in various forms. A common theme from the current work is that L-cysteine synthesis genes are seemingly up-regulated by many stresses. Thus, the authors focused on deleting two of the three L-cysteine synthesis genes (cysM and cysK2) in Mtb to better understand the roles of these genes in Mtb physiology.

The cysM and cysK2 mutants display fitness defects in various media (Sautons media, starvation, oxidative and nitrosative stress) noted by CFU reductions. Transcriptional profiling studies with the cysM and cysK2 mutants revealed that divergent gene signatures are generated in each of these strains under oxidative stress, suggesting that cysM and cysK2 have non-redundant roles in Mtb's oxidative stress response which likely reflects the different substrates used by these enzymes, CysO-L-cysteine and O-phospho-L-serine, respectively. Note that these studies lack genetic complementation and are thus not rigorously controlled for the engineered deletion mutations.

The authors quantify the levels of sulfur-containing metabolites (methionine, ergothioneine, mycothiol, mycothionine) produced by the mutants following exposure to oxidative stress. Both the cysM or cysK2 mutants produce more methionine, ergothioneine, and mycothionine relative to WT under oxidative stress. Both mutants produce less mycothiol relative to WT under the same condition. These studies lack genetic complementation and thus, do not rigorously control for the engineered mutations.

Next, the mutants were evaluated in infection models to reveal fitness defects associated with oxidative and nitrosative stress in the cysM or cysK2 mutants. In LPS/IFNg activated peritoneal macrophages, the cysM or cysK2 mutants display marked fitness defects which can be rescued with exogenous cysteine added to the cell culture media. Peritoneal macrophages lacking the NADPH oxidase (Phox) or IFNg fail to produce fitness phenotypes in the cysM or cysK2 mutants suggesting that oxidative stress is responsible for the phenotypes. Similarly, chemical inhibition of iNOS partly abrogated the fitness defect of the cysM or cysK2 mutants. Similar studies were conducted in mice lacking IFNg and Phox establishing that cysM or cysK2 mutants have fitness defects in vivo that are dependent on oxidative and nitrosative stress.

Lastly, the authors use small molecule compounds to inhibit cysteine synthases. It is demonstrated that the compounds display inhibition of Mtb growth in 7H9 ADC media. No evidence is provided to demonstrate that these compounds are specifically inhibiting the cysteine synthases via "ontarget inhibition" in the whole Mtb cells. Additionally, it is wrongly stated in the discussion that "combinations of L-cys synthase inhibitors with front-line TB drugs like INH, significantly reduced the bacterial load inside the host". This statement suggests that the INH + cysteine synthase inhibitor combinations reduce Mtb loads within a host in an infection assay. No data is presented to support this statement.

We agree with the reviewer that the experiments do not conclusively prove that these compounds specifically inhibit the cysteine synthases via "on-target inhibition" in the whole Mtb cells. However, the inhibitors used in this study have been previously profiled in vitro (https://www.sciencedirect.com/science/article/abs/pii/S0960894X17308405?via%3Dihub).  We have modified the sentence to “a combination of L-cysteine synthase inhibitors with front-line TB drugs like INH, significantly reduced the bacterial survival in vitro”

References

(1) Hatzios, S.K. and C.R. Bertozzi, The regulation of sulfur metabolism in Mycobacterium tuberculosis. PLoS Pathog, 2011. 7(7): p. e1002036.

(2) Senaratne, R.H., et al., 5'-Adenosinephosphosulphate reductase (CysH) protects Mycobacterium tuberculosis against free radicals during chronic infection phase in mice. Mol Microbiol, 2006. 59(6): p. 1744-53.

(3) Betts, J.C., et al., Evaluation of a nutrient starvation model of Mycobacterium tuberculosis persistence by gene and protein expression profiling. Mol Microbiol, 2002. 43(3): p. 717-31.

(4) Hampshire, T., et al., Stationary phase gene expression of Mycobacterium tuberculosis following a progressive nutrient depletion: a model for persistent organisms? Tuberculosis (Edinb), 2004. 84(3-4): p. 228-38.

(5) Schnappinger, D., et al., Transcriptional Adaptation of Mycobacterium tuberculosis within Macrophages: Insights into the Phagosomal Environment. J Exp Med, 2003. 198(5): p. 693-704.

(6) Voskuil, M.I., et al., The response of mycobacterium tuberculosis to reactive oxygen and nitrogen species. Front Microbiol, 2011. 2: p. 105.

(7) Voskuil, M.I., K.C. Visconti, and G.K. Schoolnik, Mycobacterium tuberculosis gene expression during adaptation to stationary phase and low-oxygen dormancy. Tuberculosis (Edinb), 2004. 84(3-4): p. 218-27.

(8) Brunner, K., et al., Profiling of in vitro activities of urea-based inhibitors against cysteine synthases from Mycobacterium tuberculosis. Bioorg Med Chem Lett, 2017. 27(19): p. 4582-4587.

(9) Manganelli, R., et al., Role of the extracytoplasmic-function sigma factor sigma(H) in Mycobacterium tuberculosis global gene expression. Mol Microbiol, 2002. 45(2): p. 365-74.

(10) Burns, K.E., et al., Reconstitution of a new cysteine biosynthetic pathway in Mycobacterium tuberculosis. J Am Chem Soc, 2005. 127(33): p. 11602-3.

(11) Manganelli, R., et al., The Mycobacterium tuberculosis ECF sigma factor sigmaE: role in global gene expression and survival in macrophages. Mol Microbiol, 2001. 41(2): p. 423-37.

(12) Tyagi, P., et al., Mycobacterium tuberculosis has diminished capacity to counteract redox stress induced by elevated levels of endogenous superoxide. Free Radic Biol Med, 2015. 84: p. 344-354.

(13) de Carvalho, L.P., et al., Metabolomics of Mycobacterium tuberculosis reveals compartmentalized co-catabolism of carbon substrates. Chem Biol, 2010. 17(10): p. 1122-31.

(14) Agapova, A., et al., Flexible nitrogen utilisation by the metabolic generalist pathogen Mycobacterium tuberculosis. Elife, 2019. 8.

(15) Khan, M.Z., et al., Redox homeostasis in Mycobacterium tuberculosis is modulated by a novel actinomycete-specific transcription factor. EMBO J, 2021. 40(14): p. e106111.

(16) Brunner, K., et al., Inhibitors of the Cysteine Synthase CysM with Antibacterial Potency against Dormant Mycobacterium tuberculosis. J Med Chem, 2016. 59(14): p. 6848-59.

(17) Wheeler, P.R., et al., Functional demonstration of reverse transsulfuration in the Mycobacterium tuberculosis complex reveals that methionine is the preferred sulfur source for pathogenic Mycobacteria. J Biol Chem, 2005. 280(9): p. 8069-78.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

(1) In Figure S1 it would be useful to include the reverse transsulfuration pathway given that it contributes to the L-cysteine pool, and that L-methionine was used for metabolite labelling experiments.

We are in agreement with the reviewer’s suggestion, and we have included reverse transsulfuration in Fig S1. Please note that Labelling was not performed with L-methionine. We used 34S derived from SO42-to monitor the reductive assimilation of sulfur and its transit from S2- until Lmethionine, passing through cysteine. We specified in material and methods that we have used sodium sulfate-34S (Merck 718882), as our label source of sulfur. This method was first employed in M. tuberculosis by the Bertozzi group to identify sulfolipids in mycobacteria. Therefore, we are not measuring transsulfuration but instead a direct synthesis of Lmethionine via cysteine, and consequently, we are indeed assessing the importance of cysK2 and cysM in this process. We have now added to the results section (page 9) that we employed (Na34SO4) for labeling to make sure other readers will not think we are measuring transulfuration.

Author response image 1.

(2) In Figure S2 it is unclear why the control is included in this figure given that the stress conditions were compared to the control. What is the control being compared to here?

The heat maps of controls have been included to demonstrate relative gene expression in independent/each of the replicates. The normalized count for the differentially expressed genes are plotted. To better understand the RNA-seq results, we plotted the fold change of differentially expressed genes due to different stress conditions (New figure & table- Figure S3 & Table S2). This allowed us to understand the expression profile of genes in all the stress conditions simultaneously, regardless of whether they were identified as differentially expressed. The data revealed that specific clusters of genes are up- and downregulated in oxidative, SDS, and starvation conditions. In comparison, the differences observed in the pH 5.5 and nitrosative conditions were limited (Figure S3 & Table S2).  

(3) In Figure S3 it would be more informative to show fold-enrichment than gene counts in (b) to (f).

In our opinion, gene counts are more informative when plotting GO enrichments, as the number of genes in each GO category can vary drastically. The significance values are already calculated based on the fold enrichment of a category compared to the background, and hence, p-adj values plotted on the x-axis can be sort of a proxy for fold enrichment. Hence, instead of plotting two related variables, plotting the total gene counts that belonged to a category is usually helpful for the reader in understanding the “scale” in which a category is affected.

(4) Figure 1c standard Sautons is a defined media, and is not nutrient-limiting - the authors should clarify the composition of the media that they used here.

The composition of Sautons media used in the study is 0.5g/L MgSO4.7H20, 2 g/L citric acid, 1g/L L-asparagine, 0.3 g/L KCl.H20, 0.2% glycerol, 0.64 g/L FeCl3, 100 μM NH4Cl and 0.7 g/L K2HPO4.3H20. We have modified the sentence in line with reviewer’s suggestion.  

(5) The authors claim that the distinct transcriptomes for the two mutants indicate that "CysM and CysK2 distinctly modulate 324 and 1104 genes". The effect is likely due to distinct downstream consequences of the deletions, rather than direct regulation by the synthases. This section should be reworded for clarity.

We have modified the sentence in line with reviewer’s suggestion.

(6) In Figure 3 it would be useful to express mycothione levels as a percentage of the total mycothiol pool to give an indication of the extent to which the thiol is being oxidised.

While we appreciate reviewer’s suggestion, we cannot make ratios of IC for two different compounds, as they ionize different. 100 ion counts of one does NOT equal to 100 ion counts of the other.

(7) Figure 6 is difficult to interpret as the concentrations used in the INH + inhibitor wells are not clear. It would be useful to indicate the concentrations of each compound added next to the wells in the figure.

We have modified the figure and legends in line with reviewer’s suggestion

Reviewer #2 (Recommendations For The Authors):

(1) Document the cysM deletion.

The details of CysM knockout generation have been previously published ([15]; Appendix Figure S4), and complementation strain details are provided in the methods section. 

(2) The oxidative stress CHP is not defined in the figure legend.

We have modified the legend in line with the reviewer’s suggestion.

(3) Can we see the structures of the compounds?

Kindly refer to Fig 6a for the structures of compounds 

(4) Fix the genetics and the paper is very interesting.

I might be missing something. The authors do provide promising complementation data for several of the stresses. Provide evidence for the cysM deletion and complementation and the data will be very compelling. The focus of the paper is important for our understanding of the biology of Mycobacterium tuberculosis.

Thank you for appreciating our study. The details of CysM knockout and complementation strain generation have been previously published ([15]; Appendix Figure S4 & Methods)). CysK2 mutant and complementation strain details are included in the present manuscript (Figure 1b & Methods).

Reviewer #3 (Recommendations For The Authors):

The transcriptional profiling studies do not rigorously control for the engineered mutations using genetic complementation.

The complementation strains used in all in vitro, ex vivo and in vivo experiments showcase that the phenotypes associated with knockouts are gene specific. We choose not to include complementation strains in RNA sequencing experiments due to the large number of samples handling and associated costs.  

Figure 3. These data are not rigorously controlled without genetic complementation, explain why some data in Figure 3 was generated at 24 hr and other data was generated at 48 hr, remove subbars in 3g. Please provide more clarification on Fig 3e-g because the normalization in these panels makes it appear as if there is little- or no-difference in the levels of 34S incorporation into the thiol metabolites.

The complementation strains used in all in vitro, ex vivo, and in vivo experiments showcase that the phenotypes associated with knockouts are gene-specific. We chose not to include complementation strains in Figure 3 experiments due to the large number of sample handling and associated costs. 

The time points in the given experiment were chosen based on an initial pilot experiment. It is apparent that a longer duration is required to see the phenotypes associated with labelling compared to pool size. The differences observed are statistically significant. 

Surfactant and SDS stress are used interchangeably in the text, legends, and figures. Please be consistent here.

We have modified the text in line with reviewer’s suggestion.

Consider re-wording the 1st paragraph on page 5 to better clarify how Trp, Lys, and His interact with the host immune cells.

We have modified the text in line with reviewer’s suggestion.

Cite the literature associated with the sulfur import system in Mtb on page 3 in the 2nd paragraph.

We have modified the text in line with reviewer’s suggestion.

The manuscript nicely describes the construction of a cysK2 mutant. It is unclear how the cysM mutant was generated. Please clarify, cite, or add the cysM mutant construction to this manuscript.

The details of CysM knockout and complementation strain generation has been previously published ([15]; Appendix Figure S4 & Methods)). We have included the citation in the methods section of current manuscript.

Provide evidence that the small molecules used in Fig 6 are on target and inhibit the cysteine biosynthetic enzymes in whole bacteria. It is unclear how a MIC can be determined with these compounds in 7H9 ADC when deletion mutants grow just fine in this media. Is this because the compounds inhibit multiple cysteine synthesis enzymes and/or enzymatic targets in other pathways? To me, the data suggests that the compounds are hitting multiple enzymes in whole Mtb cells. Does cysteine supplementation reverse the inhibitory profiles with the compounds in Figure 6?

As mentioned in the text, all the compounds were ineffective in killing Mtb, likely because Lcysteine synthases are not essential during regular growth conditions. Hence, the MIC for cysteine inhibitors was very high - C1 (0.6 mg/ml), C2 (0.6 mg/ml), and C3 (0.15 mg/ml) opposed to the standard drug, isoniazid with MIC of 0.06 ug/ml. We agree with the reviewer that the experiments do not conclusively prove that these compounds specifically inhibit the cysteine synthases via "on-target inhibition" in  Mtb cells. The inhibitors used in this study have been previously profiled in vitro [8]. However, one cannot rule out the hypothesis that these compounds might also have some off-target effects.

Author response:

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

eLife assessment

This study advances our understanding of the allosteric regulation of anaerobic ribonucleotide reductases (RNRs) by nucleotides, providing valuable new structural insight into class III RNRs containing ATP cones. The cryo-EM structural characterization of the system is solid, but some open questions remain about the interpretation of activity/binding assays and the newly incorporated HDX-MS results. The work will be of interest to biochemists and structural biologists working on ribonucleotide reductases and other allosterically regulated enzymes.

Public Reviews:

Reviewer #1 (Public Review):

The goal of this study is to understand the allosteric mechanism of overall activity regulation in an anaerobic ribonucleotide reductase (RNR) that contains an ATP-cone domain. Through cryo-EM structural analysis of various nucleotide-bound states of the RNR, the mechanism of dATP inhibition is found to involve order-disorder transitions in the active site. These effects appear to prevent binding of substrate and a radical transfer needed to initiate the reaction.

Strengths of the manuscript include the comprehensive nature of the work - including both numerous structures of different forms of the RNR and detailed characterization of enzyme activity to establish the parameters of dATP inhibition. The manuscript has been improved in a revision by performing additional experiments to help corroborate certain aspects of the study. But these new experiments do not address all of the open questions about the structural basis for mechanism. Additionally, some questions about the strength of biochemical data and fit of binding or kinetic curves to data that were raised by other referees still remain. Some experimental observations are not consistent with the proposed model. For example, why does dATP enhance Gly radical formation when the proposed mechanism of dATP inhibition involves disorder in the Gly radical domain?

The work is impactful because it reports initial observations about a potentially new mode of allosteric inhibition in this enzyme class. It also sets the stage for future work to understand the molecular basis for this phenomenon in more detail.

We express our gratitude to the reviewer for dedicating time to review our work and for the overall favorable assessment. We agree that the question of exactly how much the glycyl radical domain becomes more mobile without losing the glycyl radical entirely is an unresolved one but we also think that our work sets a solid basis for future experiments by us and others.

Reviewer #3 (Public Review):

The manuscript by Bimai et al describes a structural and functional characterization of an anaerobic ribonucleotide reductase (RNR) enzyme from the human microbe, P. copri. More specifically, the authors aimed to characterize the mechanism by how (d)ATP modulates nucleotide reduction in this anaerobic RNR, using a combination of enzyme kinetics, binding thermodynamics, and cryo-EM structural determination, complemented by hydrogen-deuterium exchange (HDX). One of the principal findings of this paper is the ordering of a NxN 'flap' in the presence of ATP that promotes RNR catalysis and the disordering (or increased protein dynamics) of both this flap and the glycyl radical domain (GRD) when the inhibitory effector, dATP, binds. The latter is correlated with a loss of substrate binding, which is the likely mechanism for dATP inhibition. It is important to note that the GRD is remote (>30 Ang) from the binding site of the dATP molecule, suggesting long-range communication of the structural (dis)ordering. The authors also present evidence for a shift in oligomerization in the presence of dATP. The work does provide evidence for new insights/views into the subtle differences of nucleotide modulation (allostery) of RNR, in a class III system, through long-range interactions.

The strengths of the work are the impressive, in-depth structural analysis of the various regulated forms of PcRNR by (d)ATP using cryo-EM. The authors present seven different models in total, with striking differences in oligomerization and (dis)ordering of select structural features, including the GRD that is integral to catalysis. The authors present several, complementary biochemical experiments (ITC, MST, EPR, kinetics) aimed at resolving the binding and regulatory mechanism of the enzyme by various nucleotides. The authors present a good breadth of the literature in which the focus of allosteric regulation of RNRs has been on the aerobic orthologues.

The addition of hydrogen-deuterium exchange mass spectrometry (HDX-MS) complements the results originating from cryo-EM data. Most notably, is the observation of the enhanced exchange (albeit quite subtle) of the GRD domain in the presence of dATP that matches the loss of structural information in this region in the cryo-EM data. The most pronounced and compelling HDX results are seen in the form of dATP-induced protection of peptides immediately adjacent to the b-hairpin at the s-site, where dATP is expected to bind based on cryo-EM. It is clear that the presence of dATP increases the rigidity of this region.

We are happy that both reviewers find the HDX-MS experiments to be a valuable addition to the existing data.

Weaknesses:

The discussion of the change in peptide mobility in the N-terminal region is complicated by the presence of bimodal mass spectral features and this may prevent detailed interpretation of the data, especially for select peptide region that shows opposite trends upon nucleotide association.

Further, the HDX data in the NxN flap is unchanged upon nucleotide binding (ATP, dATP, or CTP), despite changes observed in the cryo-EM data.

We are grateful to the reviewer for the comprehensive feedback on the HDX-MS part and for identifying areas for improvement. The HDX analysis was of course undertaken with the intention of identifying differences in disorder of the NxN flap and GRD region. From an HDX perspective both regions were found to be highly susceptible to HDX regardless of state/ligand, due to surface accessibility and/or very fast dynamics. However, this does not mean that there is no difference in the degree of order of these regions upon ligand addition, simply that we with HDX-MS, in the limited time span of 30-3000 seconds, could not conclusively support an increased disorder. We have rephrased the discussion text to reflect this fact

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

On page 5 (and throughout the manuscript) there are some inconsistencies in how dissociation constants for effectors and inhibitors are described - for example, D in KD is sometimes subscripted and sometimes not.

Thank you for noticing these remaining errors. We hope that we have fixed all of them now.

Reviewer #3 (Recommendations For The Authors):

The authors addressed many of the initial concerns raised. The addition of the HDX-MS data in this revision is a welcomed contribution to the work and complements the cryo-EM data. In select cases, the data may be over-interpreted. This reviewer suggests that the authors revise the text in this section so that it is more consistent with the presented data.

Specific points:

(1) The bimodal mass spectral features in the N-terminal domain complicate the data interpretation. Specifically for peptides in 81-99 region, the fast exchanging feature shows protection in the presence of (d)ATP/CTP, but the opposite trend is observed for the slow exchanging species. It is therefore advisable to not make absolutes about the HDX results in this region, as the data are complicated.

As stated by the reviewer, it is not possible from the presented HDX data to deduce if this is a result of 50% loaded dimer or the oligomerization state of the protein. We have remedied this by removing mentions of a difference between the dATP and ATP in bimodality. Also, we have addressed this in the text by stating that the main reason is most likely the different oligomerization states present in solution. Nevertheless, it is clear from the HDX data that the N-terminal region and 81-99 are very interesting, and it was somewhat disappointing that due to the dynamics of the oligomerization it was not possible to SEC-purify pure dimer or tetramer samples for HDX-MS, in order to deconvolute the cause.

(2) Related to #1, the authors assign the bimodal HDX behavior to EX1 mechanism, but this is not necessarily (and unlikely) true based on the limited time points. The authors also state that it originates from the heterogeneity of the sample: "a mixture of states" which could reflect the mixture of oligomerization states. The authors should be careful assigning EX1 mechanism unless there are compelling results to support it.

We apologize for the unfortunate phrasing. It was not our intention to imply that the bimodality is due to true EX1 kinetics. See the above answer. The mention of EX1 has been removed from the discussion text.

(3) The deuterium uptake for peptide 118-126 is very small (~1Da) compared to the length of the peptide. The change in deuterium uptake (<0.25Da) from dATP is very small; the authors should proceed with caution when presenting interpretations of such small differences.

We agree with the reviewer that extra caution should be taken when dealing with such a small difference. However, the 118-126 peptide has been significance tested in both HDExaminer and Deuteros 2.0, and we also observed this for more than one run. The difference in uptake is small but increases to significance at the longer labelling times. The proximity to the NxN flap makes it interesting in context of an allosteric conformational change. i.e the dynamics of the NxN might be too fast so we can only see some secondary effects. We would like to keep the data  in Figure 10 for reasons of transparency. In essence this is similar to the observed bimodality mentioned above: we cannot fully explain the observation but present the data as it was observed.

(4) On p. 22, the authors should consider revising the following statement: "confirming dATP binding to the s-site." Even though the HDX data are most compelling for the protection of peptides 178-204 and 330-348 that are adjacent to the beta-hairpin at the s-site, these data cannot "confirm" a binding site for a small molecule, such as dATP.

We appreciate that the reviewer has pointed out that the statement can be misleading, and we agree that the binding site of small molecules can’t be confirmed based solely on HDX data. The sentence reformulated to clarify that the binding site was confirmed based on the combined evidence of HDX data and the previously presented biochemical and structural data on the s-site.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Valk and Engert et al. examined the potential relations between three different mental training modules, hippocampal structure and functional connectivity, and cortisol levels (stress) over a 9-month period. They found that among the three types of mental training: Presence (attention and introspective awareness), Affect (socio-emotional - compassion and prosocial motivation), and Perspective (socio-cognitive - metacognition and perspective taking) modules; Affect training most robustly related to changes in hippocampal structure and function - specifically, CA1-3 subfields of the hippocampus. Moreover, change in intrinsic functional connectivity related to changes in diurnal cortisol release and long-term cortisol exposure. These changes are proposed to result from a combination of factors, which is supported by multivariate analyses showing changes across subfields and training content relate to cortisol changes.

The authors demonstrate that mindfulness training programs are a potential avenue for stress interventions that impact hippocampal structure and cortisol, providing a promising approach to improve health. The data contribute to the literature on plasticity of hippocampal subfields during adulthood, the impact of mental training interventions on the brain, and the link between CA1-3 and both short- and long-term stress changes.

The authors thoughtfully approached the study of hippocampal subfields, utilizing a method designed for T1w images that outperformed Freesurfer 5.3 and that produced comparable results to an earlier version of ASHS. The authors note the limitations of their approaches and provide detailed information on the data used and analyses conducted. The results provide a strong basis from which future studies can expand using computational approaches or more fine-grained investigations of the impact of mindfulness training on cortisol levels and the hippocampus.

We thank the Reviewer for the positive re-evaluation and summary of our findings and work. We made additional change as suggested and hope this clarified any open points.

I have a few additional suggestions. Clarifying the language around the multivariate results and the impact across subfields and training modules would be helpful. 

We are happy to provide further clarifications with respect to the multivariate results and the impact of training on subfields.

The multivariate analyses served as a final step to explore any potential connections between training modules and hippocampal subfields, beyond just the link between CA1-3 and the Affect Module. These additional analyses were suggested by the Reviewers, and we, as authors, agreed that taking a broader view of how different parts of the hippocampus interact with overall changes can provide valuable insights into the relationship between mental training, cortisol fluctuations, and changes in CA1-3 subfields.

We employed a multivariate partial least squares method, which aims to identify the directions in the predictor space that account for the most variance in changes observed, by creating latent variables. Initially, we investigated whether there was a general connection between CA1-3 subfields and cortisol changes, regardless of which training module produced these effects. Our findings confirmed a consistent relationship across all three training modules, indicating a strong association between cortisol changes, particularly markers such as AUC and slope change, and alterations in CA1-3 structure and functional connectivity. We explored a model incorporating changes across all hippocampal subfields and stress markers across different modules. In the right hemisphere, changes in the volume of the CA1-3 subfield were more strongly associated with stress markers, compared to other subfields. However, this association was less pronounced in the left hemisphere.

Our multivariate approach captured fluctuations across subfields and modules beyond group-level associations, leading to a more nuanced interpretation. While the univariate analysis of module-specific changes in volume and associations within the Affect Module may offer a straightforward interpretation, as they coincide with increases in CA1-3 volume, the multivariate analysis also accounts for individual-level changes not observed at the group level using a data-driven approach. Overall these findings are in line with the group-level observations, yet provide nuance on specificity.

We clarified these considerations further in the manuscript;

Abstract:

“Notably, using a multivariate approach, we found that other subfields that did not show group-level changes also contributed to changes in cortisol levels.”

Results:

“We employed a multivariate partial least squares method, which aims to identify the directions in the predictor space that account for the most variance in changes observed, by creating latent variables. Initially, we investigated whether there was a general connection between CA1-3 subfields and cortisol changes, regardless of which training module produced these effects.”

Discussion:

“Finally, through conducting multivariate analysis, we once more noticed associations between changes in CA1-3 volume and functional adaptability and alterations in stress levels, particularly prominent within the Affect Module. Integrating all subfields into a unified model highlighted a distinct significance of CA1-3, although for the left hemisphere, we observed a more diverse range of contributions across subfields. In summary, we establish a connection between a socio-emotional behavioral intervention, shifts in hippocampal subfield structure and function, and decreases in cortisol levels among healthy adults.

Although the univariate examination of changes specific to modules in volume and connections within the Affect Module presents how changes in cortisol align with group-level rises in CA1-3 volume, the multivariate analysis extended this observation through considering individual-level alterations not discernible at the group level through a data-driven method. These results generally corresponded with observations at the group level but offer additional insights into specificity, and hint at system-level alterations.”

Author response:

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

eLife assessment

This useful study tests the hypothesis that Mycobacterium tuberculosis infection increases glycolysis in monocytes, which alters their capacity to migrate to lymph nodes as monocyte-derived dendritic cells. The authors conclude that infected monocytes are metabolically pre-conditioned to differentiate, with reduced expression of Hif1a and a glycolytically exhaustive phenotype, resulting in low migratory and immunologic potential. However, the evidence is incomplete as the use of live and dead mycobacteria still limits the ability to draw firm conclusions. The study will be of interest to microbiologists and infectious disease scientists.

In response to the general eLife assessment, we would like to emphasize that the study did not deal with “infected monocytes” per se but rather with monocytes purified from patients with active TB. We show that monocytes purified from these TB patients (versus healthy controls) differentiate into DCs with different migratory capacities. In addition, to address the reviewer's comments in this new version of our manuscript, we include a relevant characterization of the migration capacity of DCs infected with Mtb to the plethora of assays already shown with viable bacteria in the previous revised version of our manuscript. 

All in all, we believe that our study has significantly improved thanks to the feedback provided by the editor and reviewer panel during the different revision processes. We sincerely hope that this version of our manuscript is deemed fit for publication in this prestigious journal.

Public Reviews:

Reviewer #3 (Public Review):

In the revised manuscript by Maio et al, the authors examined the bioenergetic mechanisms involved in the delayed migration of DC's during Mtb infection. The authors performed a series of in vitro infection experiments including bioenergetic experiments using the Agilent Seahorse XF, and glucose uptake and lactate production experiments. Also, data from SCENITH is included in the revised manuscript as well as some clinical data. This is a well written manuscript and addresses an important question in the TB field. A remaining weakness is the use of dead (irradiated) Mtb in several of the new experiments and claims where iMtb data were used to support live Mtb data. Another notable weakness lies in the author's insistence on asserting that lactate is the ultimate product of glycolysis, rather than acknowledging a large body of historical data in support of pyruvate's role in the process. This raises a perplexing issue highlighted by the authors: if Mtb indeed upregulates glycolysis, one would expect that inhibiting glycolysis would effectively control TB. However, the reality contradicts this expectation. Lastly, the examination of the bioenergetics of cells isolated from TB patients undergoing drug therapy, rather than studying them at their baseline state is a weakness.

We thank the reviewer for this insightful assessment and feedback of our study. With regards to the data obtained with iMtb to support that with live Mtb, we have clarified the use of either iMtb or Mtb for each figure legend in the new version of the manuscript. Furthermore, we included the confirmation of the involvement of TLR2 ligation in the up-regulation of HIF-1α triggered by viable Mtb (new Fig S2E). We also conducted migration assays using (live) Mtb-infected dendritic cells (DCs) treated with either oxamate or PX-478 to validate that the HIF1a/glycolysis axis is indeed essential for DC migration (new Fig 5D).

We respectfully acknowledge the reviewer's statement regarding the potential relationship between glycolysis and the control of TB. However, we find it necessary to elaborate on our stance, as our data offer a nuanced perspective. Our research indicates that DCs exhibit upregulated glycolysis following stimulation or infection by Mtb. This metabolic shift is crucial for facilitating cell migration to the draining lymph nodes, an essential step in mounting an effective immune response. Yet, it remains uncertain whether this glycolytic induction reaches a threshold conducive to generating a protective immune response, a matter that our findings do not definitively address. This aspect is carefully discussed in the manuscript, lines 380-385.

Moreover, analyses of samples from chronic TB patients suggest that the outcome of inhibiting glycolysis may vary depending on factors such as the infection stage, the targeted cell type (e.g., monocytes, DCs), and the affected compartment (systemic versus local). This variability aligns with the concept of "too much, too little" exemplified by the dual roles of IFNγ (PMID: 28646367) and TNFα (PMID: 19275693) in TB, emphasizing the need to maintain an inflammatory equilibrium. In the context of the HIF1α/glycolysis axis, it appears to be a matter of timing: a case of "too early" activation of glycolysis in precursors, which could upset the delicate balance necessary for an effective immune response. We have added these comments in the discussion (pages 19-20, lines 468-485).

In summary, while acknowledging the reviewer's perspective, we believe that a comprehensive understanding of the interplay between Mtb infection and glycolysis in myeloid cells requires further consideration of various contextual conditions, urging caution against oversimplified interpretations.

With regard to the patients' information, as pointed out by the reviewer, according to the inclusion criteria for patient samples in the approved protocol by the Institutional Ethics Committee, we recruit patients who have received less than 15 days of treatment (for sensitive TB, the total treatment duration is at least 6 months). We do not have access to patient sample before they begin the treatment, as starting therapy is the most urgent matter in this case. Following the reviewer's suggestion, we investigated whether the glycolytic activity of monocytes correlated with the initiation of antibiotic treatment within this 15-day period. Our observations did not show any significant impact during the initial 15 days of treatment (see expanded reply below). However, after 2 months of treatment, we found that the glycolytic profile of CD16+ monocytes returned to baseline levels as per our analysis. This suggests that despite the normalization of glycolytic activity with antibiotic therapy, heightened basal glycolysis remains noticeable during the initial two weeks of treatment (time limit to meet the inclusion criteria in our study cohort).

Recommendations for the authors:

Reviewer #3 (Recommendations For The Authors):

(1) In the revised manuscript, the authors addressed concerns related to using irradiated Mtb, a positive development. However, the study predominantly employs 1:1 or 2:1 MOI, representing a low infection model, with no observed statistical distinction between the two MOIs (Fig-1). To enhance the study, inclusion of a higher MOI (e.g., 5:1 or 10:1) would have been more informative. This becomes crucial as prior research on human macrophages indicates that Mtb infection typically hampers glycolysis, a finding inconsistent with the present study.

As the reviewer notes, important work has documented the inhibition of glycolysis in M. tuberculosis-infected macrophages dependent on the MOI (PMID 30444490). For instance, in this study, hMDMs infected at an MOI of 1 showed increased extracellular acidification and glycolytic parameters, as opposed to macrophages infected at higher MOI, or the same MOI but measured in THP1 cells. In light of these findings, we attempted to extend our study with Mo-DCs to higher MOIs, but too much cell death was induced, limiting our ability to obtain reliable metabolic measurements and functional assays from these cultures. Consistent with this, other authors reported that more than 40% of Mo-DC die after 24 hours following infection with H37Rv at an MOI of 10 (PMID 22024399, Fig 2B). We acknowledge that more comprehensive focused in vivo studies would be needed to assess the overall impact of infection. We foresee that in the context of natural infection, DC with different levels of infection will coexist, some with low bacillary load that may be able to trigger glycolysis and migrate, others highly infected and more likely to die. In this case, we are unable to provide a full explanation for the delay in the onset of the adaptive response, an aspect that requires further investigation. From our perspective, the important contribution of our work is more focused on understanding the later stage of infection, when chronic infection is established, where precursors already seem to have a limited capacity to generate DC with a good migratory performance regardless of being confronted with a low bacillary load. 

To better clarify the scope and limitations of the work, we added these comments to the discussion (see discussion, lines 405-408).

The study emphasizes that Mtb infection enhances glycolysis in Mo-DCs (Fig-1 and Fig-2). Despite the authors advocating lactate as the end product (citing three reviews/opinions), the historical literature supported by detailed experimentation convincingly favors pyruvate. While the authors' attempt to support an alternate glycolytic paradigm is understandable, it is simply not necessary. This is further supported by the authors' claim that oxamate is an inhibitor of glycolysis (abstract and main text). Oxamate is a pyruvate analogue that directly inhibits the conversion of pyruvate into lactate by lactate dehydrogenase. Simply put, if oxamate was an inhibitor of glycolysis then the cells would have died.

(2) Taking into account the reviewer's suggestions, we changed the text accordingly, referring to oxamate as an LDH inhibitor, including in the abstract.

In Fig-2, clarify the term "bystander DCs." Explain why these MtbRFP- DCs exhibit distinct behavior compared to uninfected DCs, especially considering their similarity to Mtb-infected ones.

(3) To clarify these results, as correctly suggested by the reviewer, we incorporated a sentence in the results section, stating that bystander DCs are cells that are not in direct association with Mtb (Mtb-RFP-DCs), but are rather nearby and exposed to the same environment (page 7, line 145-148). In other words, bystander cells are those exposed to the same secretome and soluble factors as infected cells. Our data indicate that bystander DCs upregulate their state of glycolysis just like infected DCs do, which suggests the presence of soluble mediators induced during infection that are capable of triggering glycolysis even in uninfected cells.

These results are in line with the observation that bacteria lacking infectious capacity (such as the irradiated Mtb) also trigger glycolysis in DCs (Fig 1), likely via TLR2 receptors that are potentially activated by the release of mycobacterial antigens or bacterial debris present in the microenvironment (Fig 3). We incorporated this interpretation in the discussion of the manuscript (lines 403-408).

(4) Notably, the authors conducted SCENITH on both iMtb and viable Mtb (Fig-2). However, OCR, PER, and Mito- & Glyco- ATP were solely measured in MO-DCs stimulated by iMtb. Given the distinct glycolytic responses between iMtb and viable Mtb, it is crucial to assess these parameters in Mo-DCs treated with viable Mtb. Moreover, it is unclear as to how the relative ATP in Fig-2F was calculated as both Mito-ATP and Glyco-ATP is significantly high in iMtb-treated Mo-DCs (Fig-2E). Also, figure 2 contains panels with no labeling, which is confusing.

We appreciate the reviewer's suggestion that additional determinations would enrich the bioenergetic profile of DCs during infection. However, due to biosafety considerations and economic-driven limitations, we are currently unable to measure OCR, PER, and Mito- & Glyco- ATP, as these assessments require live cell cultures within BSL3 containment, if live Mtb is to be employed. Regrettably, our BSL3 facility is not equipped with a Seahorse instrument—few facilities in the world have such type of BLS3-driven investment. For this key reason, we employed SCENITH for our BSL3-based experiments.

Concerning the how ATP was calculated, we show below the raw data for Mito-ATP and Glyco-ATP results and calculations of their relative contributions.

Author response table 1.

(5) In Figures 3, 4, & 5, the consistent use of only iMtb was observed. Previous concerns about this approach were raised in the review, with the authors asserting that the use of viable Mtb was beyond the manuscript's scope. However, this claim is inaccurate. Both the authors' findings and literature elsewhere emphasize notable differences not only in host-cell metabolism but also in immune responses when treated with viable Mtb compared to dead or iMtb. Therefore, it is recommended to incorporate viable Mtb in experiments where only iMtb was utilized. Also, in the abstract (3rd sentence), do the authors refer to live or irradiated Mtb? It is imperative to clearly indicate this distinction, as the subsequent conclusions are based only on one of these two scenarios, not both. The contradictory mitochondrial mass results (figure 1; live and dead Mtb showed opposite mitochondrial mass results) clearly illustrate the profound difference live (versus dead) Mtb cells can have on an experiment.

We thank the reviewer for stating this concern. For Figure 3, the involvement of TLR2 ligation on lactate release was also confirmed with live Mtb (shown in Figure S2D). In this current version, we also confirmed the involvement of TLR2 ligation in the up-regulation of HIF-1α triggered by live Mtb (new Fig S2E). As for Figure 4, we agree that performing assays with live Mtb will add complementary information. Indeed, we hope to investigate in the future the impact of the glycolysis/HIF1a axes on the adaptive immune response. We believe that employing live bacteria and considering their active immune evasion strategies will be crucial. However, at present, this is not the focus of the current manuscript and is beyond its scope.

We also agree with the reviewer that confirmation of the migratory behavior of DCs following Mtb infection is a crucial aspect of the study. To comply with this pertinent request, we performed new migration assays using Mtb-infected DCs treated with oxamate or PX-478 to validate that the HIF1a/glycolysis axis; results convincingly demonstrate that this axis is essential for DC migration, particularly in the context of Mtb-infected cells (new Fig 5D). Having observed the same inhibitory effect of HIF1a and LDH inhibition on cell migration in either Mtb-infected or iMtb-stimulated DCs, we consider that the sentence alluded to by the reviewer in the abstract is now applicable to both contexts (page 2, line 34-36). We hope this reviewer agrees.

(6) The discussion and the graphical abstract elucidating the distinctions in glycolysis between CD16+ monocytes of HS and TB patients and iMtb-treated Mo-DCs are currently confusing and require clarification. According to the abstract, monocytes from TB patients exhibit heightened glycolysis, resulting in diminished HIF-a activity and migratory capacity of MO-DCs. This prompts a question: if exacerbated glycolysis in monocytes is associated with adverse outcomes, wouldn't it be logical to consider suppressing glycolysis? If so, how can inhibiting glycolysis, a favored metabolic pathway for pro-inflammatory responses, be beneficial for TB therapy?

We understand the reviewer’s concern about this apparent paradox. As previously mentioned in response to the public review provided by the reviewer, inhibiting glycolysis may yield varying outcomes depending on the stage of infection, as well as the cellular target (e.g., monocytes, DCs) or compartment (systemic versus local). It is imperative to delve deeper into the potential role of the HIF1α/glycolysis axis at the systemic level within the context of chronic inflammation, contrasting with its role in a local setting during the acute phase of infection.

A comprehensive understanding of the interplay between Mtb infection and glycolysis in myeloid cells requires further consideration of various contextual conditions, urging caution against oversimplified interpretations. For instance, one of the objectives of host-directed therapies (HDTs) is to mitigate host-response inflammatory toxicity, which can impede treatment efficacy (doi: 10.3389/fimmu.2021.645485). In this regard, traditional anti-inflammatory drugs such as non-steroidal anti-inflammatory drugs (NSAIDs) and corticosteroids have been explored as adjunct therapies due to their immunomodulatory properties. Additionally, compounds like vitamin D, phenylbutyrate (PBA), metformin, and thalidomide, among others, have been investigated in the context of TB infections (doi:10.3389/fimmu.2017.00772), highlighting the diverse range of strategies aimed at enhancing TB treatment. These efforts extend beyond bolstering antimicrobial activity to encompass minimizing inflammation and mitigating tissue damage.

(7) I am not convinced that BubbleMap made any significant contribution to the manuscript perhaps because it is poorly described in the figure legends/main text (I am unable to determine what data set is significant or not).

We agree with the reviewer’s comment. To clarify the valuable information gleaned from these analyses, we have added interpretive guidelines on bubble color, bubble size and statistical significance in the legend of Figure 7. We hope these changes may reflect the significant contribution of the BubbleMap analysis approach to this study, which demonstrates a significant enrichment of interferon response gene expression in the monocyte compartment from patients with active TB compared to their control counterparts. Notably, this enrichment does not extend to genes associated with the OXPHOS hallmark.

(8) The use of cells/monocytes from TB patients is a concern in addition to the incomplete demographic table. In the case of the latter, absolute numbers including percentages should be included. Importantly, it appears that cells from TB patients were used, that received anti-TB drug therapy (regimen not stated) up to two weeks post diagnosis and not at baseline. This is important as recent studies have shown that anti-TB drugs modulates the bioenergetics of host cells. Lastly, what were the precise TB symptoms the authors referred to in figure 7C?

We have updated the demographic table and included the absolute numbers. We concur with the reviewer's viewpoint, particularly in light of recent findings illustrating the impact of anti-TB drug treatment on cell metabolism (doi: 10.1128/AAC.00932-21/). Again, this study underscores the complexity of such effects, which exhibit considerable variability influenced by factors such as cell type, drug concentration, and combination therapy.

Despite this variability, our analysis involving monocytes from TB patients, who received different antibiotic combinations within short time frames (less than 15 days) reveals a marked increase in glycolysis in CD16+ monocytes compared to healthy counterparts. We did not observe a correlation between monocyte glycolytic capacity and the start time of antibiotic treatment within this 15-day window (see below, Author response image 1). These findings suggest that the antibiotic regimen does not have a significant impact on monocyte glycolytic capacity during the first 15 days.  However, we did observe an effect of antibiotic treatment when comparing patients before and 2 months after treatment. Enrichment analysis of various monocyte subsets before and after 2 months of treatment (GEO accession number: GSE185372) showed that CD14dim CD16+ and CD14+ CD16+ populations had higher glycolytic activity before treatment, which is decreased then post-treatment (Author response image 2).

Author response image 1.

Correlation analysis between the baseline glycolytic capacity and the time since treatment onset for each monocyte subset (CD14+CD16-, CD14+CD16+ and CD14dimCD16+, N = 11). Linear regression lines are shown. Spearman’s rank test. The data are represented as scatter plots with each circle representing a single individual.

Author response image 2.

Gene enrichment analysis for glycolytic genes on the pairwise comparisons of each monocyte subset (CD14+CD16-, CD14+CD16+ and CD14dimCD16+) from patients with active TB pre-treatment vs patients with active TB (TB) undergoing treatment for 2 months. Comparisons with a p-value of less than 0.05 and an FDR value of less than 0.25 are considered significantly different.

Overall, our results indicate that while drug treatment does affect cell bioenergetics, this effect is not prominent within the first 15 days of treatment. CD16+ monocytes maintain high basal glycolytic activity that normalizes after treatment, contrasting with the CD16- population (even under the same circulating antibiotic doses). This highlights the intricate interplay between anti-TB drugs and cellular metabolism, underscoring the need for further research to understand the underlying mechanisms and therapeutic implications.

Finally, the term symptoms evolution refers to the time period during which a patient experiences cough and phlegm for more than 2-3 weeks, with or without sputum that may (or not) be bloody, accompanied by symptoms of constitutional illness (e.g, loss of appetite, weight loss, night sweats, general malaise). As requested, this definition has been included in the method section (page 28-29, lines 705-709).

Minor:

(1) Incorporate the abbreviation for tuberculosis "(TB)" in the first line of the abstract and similarly introduce the abbreviation for Mycobacterium tuberculosis when it is first mentioned in the abstract.

Thank you, we have amended it accordingly.

(2) As the majority of experiments are in vitro, the authors should specify the number of times each experiment was conducted for every figure.

We have included this information in each figure legend (see N for each panel). Since the majority of our approaches are conducted in vitro using primary cell cultures (specifically, human monocyte-derived DCs), we utilized samples from four to ten independent donors, not replicates, in order to account for the variability seen between donors.

(3) Rename Fig-2. Ensure consistent labeling for the metabolic dependency of uninfected, Mtb-infected, and the Bystander panel, aligning with the format used in panels A & B. Similarly, replace '-' with 'uninfected'.

We have modified the figure following most of the reviewer’s suggestions. However, we decided to keep the nomenclature “-” to denote a control condition, which can be unstimulated (panels A-B, fig 2) or uninfected cells (panels C-D, fig 2) depending on the experimental design.

(4) Discussion: It is unclear what the authors mean by 'some sort of exhausted glycolytic capacity'.

We have slightly modified the phrase.

Author response:

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

eLife assessment

This manuscript reports important in vitro biochemical and in planta experiments to study the receptor activation mechanism of plant membrane receptor kinase complexes with non-catalytic intracellular kinase domains. Several lines of evidence convincingly show that one such putative pseudokinase, the immune receptor EFR achieves an active conformation following phosphorylation by a co-receptor kinase, and then in turn activates the co-receptor kinase allosterically to enable it to phosphorylate down-stream signaling components. This manuscript will be of interest to scientists focusing on cell signalling and allosteric regulation.

We wish to clarify that EFR is itself, not a pseudokinase. We could show in previous work (Bender et al., 2021; https://doi.org/10.1073/pnas.2108242118 ) that EFR has catalytic activity in vitro. This catalytic activity is, however, not required for elf18-induced immune signaling in planta.

Public Reviews:

Reviewer #1 (Public Review):

Summary

The authors use an elegant but somewhat artificial heterodimerisation approach to activate the isolated cytoplasmic domains of different receptor kinases (RKs) including the receptor kinase BRI1 and EFR. The developmental RK BRI1 is known to be activated by the co-receptor BAK1. Active BRI1 is then able to phosphorylate downstream substrates. The immune receptor EFR is also an active protein kinase also activated by the co-receptor BAK1. EFR however appears to have little or no kinase activity but seems to use an allosteric mechanism to in turn enable BAK1 to phosphorylate the substrate kinase BIK1. EFR tyrosine phosphorylation by BAK1 appears to trigger a conformational change in EFR, activating the receptor. Likewise, kinase activating mutations can cause similar conformational transitions in EFR and also in BAK1 in vitro and in planta.

We wish to clarify that we make no strong link between tyrosine phosphorylation and the conformational change leading to activation of the complex. Rather, the HDX-MS data demonstrate the structural importance of Tyr836 for the activation mechanism. At present, we do not know how phosphorylation of the residue would affect the activation process.

Strengths:

I particularly liked The HDX experiments coupled with mutational analysis (Fig. 2) and the design and testing of the kinase activating mutations (Fig. 3), as they provide novel mechanistic insights into the activation mechanisms of EFR and of BAK1. These findings are nicely extended by the large-scale identification of EFR-related RKs from different species with potentially similar activation mechanisms (Fig. 5).

Weaknesses:

In my opinion, there are currently two major issues with the present manuscript. (1) The authors have previously reported that the EFR kinase activity is dispensible for immune signaling (https://pubmed.ncbi.nlm.nih.gov/34531323/) but the wild-type EFR receptor still leads to a much better phosphorylation of the BIK1 substrate when compared to the kinase inactive D849N mutant protein (Fig. 1). (2) How the active-like conformation of EFR is in turn activating BAK1 is poorly characterized, but appears to be the main step in the activation of the receptor complex. Extending the HDX analyses to resting and Rap-activated receptor complexes could be a first step to address this question, but these HDX studies were not carried out due to technical limitations.

Overall this is an interesting study that aims to advance our understanding of the activation mechanisms of different plant receptor kinases with important functions in plant immunity.

Reviewer #2 (Public Review):

Summary:

Transmembrane signaling in plants is crucial for homeostasis. In this study, the authors set out to understand to what extent catalytic activity in the EFR tyrosine kinase is required in order to transmit a signal. This work was driven by mounting data that suggest many eukaryotic kinases do not rely on catalysis for signal transduction, relying instead on conformational switching to relay information. The crucial findings reported here involve the realisation that a kinase-inactive EFR can still activate (ie lead to downstream phosphorylation) of its partner protein BAK1. Using a convincing set of biochemical, mass spectrometric (HD-exchange) and in vivo assays, the team suggest a model in which EFR is likely phosphorylated in the canonical activation segment (where two Ser residues are present), which is sufficient to generate a conformation that can activate BAK1 through dimersation. A model is put forward involving C-helix positioning in BAK1, and the model extended to other 'non-RD' kinases in Arabidopsis kinases that likely do not require kinase activity for signaling.

We prefer not to describe EFR as a tyrosine kinase. It may be the case that EFR can function under certain conditions as a dual-specificity protein kinase, but this has never been demonstrated experimentally. We therefore describe EFR as a Ser/Thr protein kinase, since it is known that the isolated cytoplasmic domain can phosphorylate on Ser and Thr residues (Wang et al., 2014; https://doi.org/10.1016/j.jprot.2014.06.009).

Strengths:

The work uses logical and well-controlled approaches throughout, and is clear and convincing in most areas, linking data from IPs, kinase assays (including clear 32P-based biochemistry), HD-MX data (from non-phosphorylated EFR) structural biology, oxidative burst data and infectivity assays. Repetitions and statistical analysis all appear appropriate.

Overall, the work builds a convincing story and the discussion does a clear job of explaining the potential impact of these findings (and perhaps an explanation of why so many Arabidopsis kinases are 'pseudokinases', including XPS1 and XIIa6, where this is shown explicitly).

Weaknesses:

No major weaknesses are noted from reviewing the data and the paper follows a logical course built on solid foundations; the use of Tables to explain various experimental data pertinent to the reported studies is appreciated.

(1) The use of a, b,c, d in Figures 2C and 3C etc is confusing to this referee, and is now addressed in the latest version

(2) The debate about kinase v pseudokinases is well over a decade old. For non-experts, the kinase alignments/issues raised are in PMID: 23863165 and might prove useful if cited.

We have cited the suggested reference in the second paragraph of the discussion.

(3) Early on in the paper, the concept of kinases and pseudokinases related to R-spine (and extended R-spine) stability and regulation really needs to be more adequately introduced to explain what comes next; e.g. some of the key work in this area for RAF and Tyr kinases where mutual F-helix Phe amino acid changes are evaluated (conceptually similar to this study of the E-helix Tyr to Phe changes in EFR) should be cited (PMID: 17095602, 24567368 and 26925779).

As an alternative, we have amended the text in several places to focus on conformational toggling between active/inactive states rather than R-spine stability. We think that this keeps the message of our manuscript focused. We hope that the reviewer finds this acceptable.

(4) In my version, some of the experimental text is also currently in the wrong order (and no page numbers, so hard for me to state exactly where in the manuscript); However, I am certain that Figure 2C is mentioned in the text when the data are actually shown in Figure 3C for the EFR-SSAA protein.

Indeed, some references to Figure 2 in the text were incorrect. We have corrected these. References in the text to Figure 3 and the data reported therein are correct.

(5) Tyr 156 in PKA is not shown in Supplement 1, 2A as suggested in the text; for readers, it will be important to show the alignment of the Tyr residue in other kinases; this has been updated in the second version. Although it is clearly challenging to generate phosphorylated EFR (seemingly through Codon-expansion here?), it appears unlikely that a phosphorylated EFR protein, even semi-pure, couldn't have been assayed to test the idea that the phosphorylation drives/supports downstream signaling. What about a DD or EE mutation, as commonly used (perhaps over-used) in MEK-type studies?

Our aim with codon expansion was to generate recombinant protein carrying high-stoichiometry phosphorylation at sites which we have previously documented to be required for downstream signaling (Macho et al., 2014; Bender et al., 2021). We additionally demonstrated previously that a DD mutant of the activation loop sites in EFR does not fully complement the efr-1 mutant (Bender et al., 2021), suggesting that the Asp mutations are not good phospho-mimics in this context. We therefore did not generate DD or EE mutations for in vitro studies.

Impact:

The work is an important new step in the huge amount of follow-up work needed to examine how kinases and pseudokinases 'talk' to each other in (especially) the plant kingdom, where significant genetic expansions have occurred. The broader impact is that we might understand better how to manipulate signaling for the benefit of plants and mankind; as the authors suggest, their study is a natural progression both of their own work, and the kingdom-wide study of the Kannan group.

Reviewer #3 (Public Review):

The study presents strong evidence for allosteric activation of plant receptor kinases, which enhances our understanding of the non-catalytic mechanisms employed by this large family of receptors.

Plant receptor kinases (RKs) play a critical role in transducing extracellular signals. The activation of RKs involves homo- or heterodimerization of the RKs, and it is believed that mutual phosphorylation of their intracellular kinase domains initiates downstream signaling. However, this model faces a challenge in cases where the kinase domain exhibits pseudokinase characteristics. In their recent study, Mühlenbeck et al. reveal the non-catalytic activation mechanisms of the EFR-BAK1 complex in plant receptor kinase signaling. Specifically, they aimed to determine that the EFR kinase domain activates BAK1 not through its kinase activity, but rather by utilizing a "conformational toggle" mechanism to enter an active-like state, enabling allosteric trans-activation of BAK1. The study sought to elucidate the structural elements and mutations of EFR that affect this conformational switch, as well as explore the implications for immune signaling in plants. To investigate the activation mechanisms of the EFR-BAK1 complex, the research team employed a combination of mutational analysis, structural studies, and hydrogen-deuterium exchange mass spectrometry (HDX-MS) analysis. For instance, through HDX-MS analysis, Mühlenbeck et al. discovered that the EFR (Y836F) mutation impairs the accessibility of the active-like conformation. On the other hand, they identified the EFR (F761H) mutation as a potent intragenic suppressor capable of stabilizing the active-like conformation, highlighting the pivotal role of allosteric regulation in BAK1 kinase activation. The data obtained from this methodology strengthens their major conclusion. Moreover, the researchers propose that the allosteric activation mechanism may extend beyond the EFR-BAK1 complex, as it may also be partially conserved in the Arabidopsis LRR-RK XIIa kinases. This suggests a broader role for non-catalytic mechanisms in plant RK signaling.

The allosteric activation mechanism was demonstrated for receptor tyrosine kinases (RTKs) many years ago. A similar mechanism has been suggested for the activation of plant RKs, but experimental evidence for this conclusion is lacking. Data in this study represent a significant advancement in our understanding of non-catalytic mechanisms in plant RK signaling. By shedding light on the allosteric regulation of BAK1, the study provides a new paradigm for future research in this area.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The authors have considered points 1-5 raised in my initial review and the revised manuscript contains a more balanced discussion and limitation section. No additional experiments have been performed to substantiate the envisioned allosteric activation mechanism of the co-receptor kinase BAK1 by the receptor EFR. I rewrote the public statement accordingly.

Reviewer #2 (Recommendations For The Authors):

Thanks for responding to my comments.

Reviewer #3 (Recommendations For The Authors):

The revised manuscript has fully addressed my previous concerns and is now suitable for publication in eLife.

Author response:

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

Key Considerations:

There seem to be two inconsistencies related to some results depicted in Figures 1, 2, 3 and 5.

Firstly, Figure 1 shows the effect on C_Las infection (_C_Las+) compared to the control (_C_Las-), where results show an increase of TAG, Glycogen, lipid droplet size, oviposition period, and fecundity. In Figures 2, 3, and 5, the authors establish the involvement of the genes _DcAKH, DcAKHR, and miR34 in this process, by showing that by preventing the function of these three factors the effects of _C_Las+ are lost. However, while Figure 1 shows the increase of TAG and lipid droplet size in _C_Las+, Figures 2, 3, and 5 do not show a significant elevation in TAG when comparing _C_Las- and _C_Las+.

Secondly, in addition to the absence of statistical difference in TAG and lipid droplet size observed in Figure 1, Figures 2, 3, and 5 show an increase in TAG and lipid droplet size after ds_DcAKH_ (Figure 2), ds_DcAKHR_ (Figure 3) and agomiR34 (Figure 5) treatments. Considering that AKH, AKHR, and miR34 are important factors to _C_Las-induce increase in TAG and lipid droplet size, one might expect a reduction in TAG and lipid droplet size when _C_Las+ insects are silenced for these factors, contrary to the observed results.

Thanks for your excellent suggestion. Lipid droplets are cellular organelles responsible for storing lipids within cells, playing a crucial role in fat metabolism and energy homeostasis. The formation and breakdown of lipid droplets involve a complex interplay of genes and enzymes, including DGAT (for synthesis), ATGL and HSL (for breakdown). In C_Las-negative _D. citri, there is a delicate balance between creasing and breaking down of lipid droplets. The enlargement of lipid droplet size following C_Las infection may result from a significantly higher synthesis rate compared to breakdown, as more energy is required during early ovarian development. The hormone AKH, a key player in fat metabolism, primarily stimulates fat breakdown. Therefore, when _DcAKH and DcAKHR are silenced without affecting fat synthesis, there is no enhancement of fat breakdown; instead, there is an accumulation of lipid droplets, resulting in their enlargement. This suggests that _C_Las infection affects both the breakdown and synthesis of lipid droplets, while AKH and AKHR primarily impact the breakdown, leading to similar outcomes. However, the underlying physiological mechanisms warrant further in-depth exploration.

Reviewer #1 (Recommendations For The Authors):

(1) Line 25: change "In addition" to "Additionally".

Thanks for your wonderful suggestion. We have changed “In addition” to “Additionally” in our revised manuscript (Line 26).

(2) Lines 60-72: Have there been any previous reports on the interaction between host AKH hormones and microorganisms in insects or animals? If yes, please add more background.

Thanks for your wonderful suggestion. We have added the interactions between host AKH hormones and microorganisms in insects (Line 74-81).

(3) Lines 82-95: add the following reference about the miR-275 of Diaphorina citri in the background. Nian, X., Luo, Y., He, X., Wu, S., Li, J., Wang, D., Holford, P., Beattie, G. A. C., Cen, Y., Zhang, S., & He, Y. (2024). Infection with 'Candidatus Liberibacter asiaticus' improves the fecundity of Diaphorina citri aiding its proliferation: A win-win strategy. Molecular Ecology, 33, e17214.

Thanks for your wonderful suggestion. We have added the sentence “in D. citri-C_Las interaction, _C_Las hijacks the JH signaling pathway and host miR-275 that targets the _vitellogenin receptor (DcVgR) to improve D. citri fecundity, while simultaneously increasing the replication of C_Las itself, suggesting a mutualistic interaction in _D. citri ovaries with _C_Las” in our revised manuscript (Line 97-100).

(4) In the figures of Nile red staining, the digit of the scale bar should be added.

Thanks for your wonderful suggestion. We have added the digit of the scale bar for Nile red staining in the Figure 1C, 2E, 3E, 5C.

(5) In Figures 2G-H, 3G-H, 5E-F, the presentation of data should be consistent with Figure 1D-E.

Thanks for your wonderful suggestion. We have changed figure 1D-E in our revised manuscript.

(6) In the discussion part, more information should be added about miR-275 and DcVgR from the above reference.

Thanks for your wonderful suggestion. We have added the information “In D. citri-C_Las interaction, _C_Las operates host hormone signaling and miRNA to mediate the mutualistic interaction between _D. citri fecundity and its replication” in Line 350-353.

(7) For the primer specific, please add the melting curves for qPCR primers of DcAKH, DcAKHR, Dcβ-ACT, U6, and miR-34 in the supplementary material.

Thanks for your wonderful suggestion. We have added the melting curves for qPCR primers of DcAKH, DcAKHR, Dcβ-ACT, U6 and miR-34 in the supplementary material of Figure S6.

(8) Line 476: Dcβ-ACT was indicated as a gene and should be Italic.

Thanks for your wonderful suggestion. We have changed “DcβACT” to “Dcβ-ACT” in our revised manuscript (Line 491).

(9) Reference style should be consistent and correct. Like [5], [10], [37], [47].

Thanks for your wonderful suggestion. We have revised them in our revised manuscript.

Reviewer #2 (Recommendations For The Authors):

(1) In order to better engage readers, I suggest emphasizing the "enhanced fecundity" in the title. A suggestion for the revised title is: Adipokinetic hormone signaling mediates the enhanced fecundity of Diaphorina citri infected by 'Candidatus Liberibacter asiaticus'.

Thanks for your wonderful suggestion. We have changed the title to “Adipokinetic hormone signaling mediates the enhanced fecundity of Diaphorina citri infected by 'Candidatus Liberibacter asiaticus'” in our revised manuscript.

(2) For the abstract, in lines 14-15, please change the first sentence to "Diaphorina citri serves as the primary vector for 'Candidatus Liberibacter asiaticus' (C_Las), the bacterium associated with the severe Asian form of huanglongbing." In line 18, delete "present". In line 19, change "increased" to "increasing". In line 21, change "triacylglycerol accumulation" to "the accumulation of triacylglycerol". In line 33, change "in _D. citri ovaries with C_Las" to "between _C_Las and _D. citri ovaries".

Thanks for your wonderful suggestion. We have revised them following your suggestion in our revised manuscript, including changed “Diaphorina citri is the primary vector of the bacterium, ‘Candidatus Liberibacter asiaticus’ (C_Las) associated with the severe Asian form of huanglongbing” to “_Diaphorina citri serves as the primary vector for 'Candidatus Liberibacter asiaticus' (C_Las), the bacterium associated with the severe Asian form of huanglongbing” in Line 15-16; deleted "present" in Line 19; changed "increased" to "increasing" in Line 20; changed "triacylglycerol accumulation" to "the accumulation of triacylglycerol" in Line 22; changed "in _D. citri ovaries with C_Las" to "between _C_Las and _D. citri ovaries" in Line 34.

(3) In lines 57-59, change "How D. citri maintains a balance between lipid metabolism and increased fecundity after infection with C_Las is not known." to "However, the mechanism of how _D. citri maintains a balance between lipid metabolism and increased fecundity after infection with _C_Las remains unknown.".

Thanks for your wonderful suggestion. We have changed " How D. citri maintains a balance between lipid metabolism and increased fecundity after infection with C_Las is not known" to "However, the mechanism of how _D. citri maintains a balance between lipid metabolism and increased fecundity after infection with _C_Las remains unknown" in our revised manuscript (Line 58-60).

(4) In Figure 1, "n.s" should be changed to "n.s.", "n.s." should be added in 13 DAE of Figure 1A, and the specific numerical value of the scale bar should be indicated on Figures 1C, 2E, 3E, and 5C.

Thanks for your wonderful suggestion. We have revised them in our revised manuscript.

(5) In all the figure legends, the "**P < 0.01,***P < 0.001" should be changed to "**p < 0.01,***p < 0.001".

Thanks for your wonderful suggestion. We have revised them in our revised manuscript.

(6) In Figures 1D-E, the preoviposition period and oviposition period were presented using a box diagram, but in other figures (including Figure 2G-H, Figure 3G-H, Figure 5E-F) these were shown using a column chart. Please keep the method of presentation consistent.

Thanks for your wonderful suggestion. We have revised the figure 1D-E in our revised manuscript.

(7) For discussion, in line 333, change "Increasing numbers" to "An increasing number". In line 334, change "vertically transmitted" to "transmitted vertically".

Thanks for  your wonderful suggestion. We have changed "Increasing numbers" to "An increasing number" in Line 345; changed "vertically transmitted" to "transmitted vertically" in Line 346 in our revised manuscript.

(8) In lines 338-342, change "There are few studies on the mechanisms underlying vector-bacteria interactions. However, Singh and Linksvayer (2020) [38] found that Wolbachia-infected colonies of Monomorium pharaonis had increased colony-level growth, accelerated colony reproduction, and shortened colony life cycles compared to those that were uninfected." to "Although there is limited research on the mechanisms underlying vectorbacteria interactions, Singh and Linksvayer (2020) [38] found that Wolbachia_infected colonies of _Monomorium pharaonis exhibited increased colony-level growth, accelerated colony reproduction, and shortened colony life cycles compared to uninfected colonies.".

Thanks for your wonderful suggestion. We have revised it in our revised manuscript (Line 350-355) .

(9) In line 370, delete "present". In lines 386-387, change "More and more miRNAs have been reported to be involved in the metabolic processes of insects including reproduction." to "There is increasing evidence implicating miRNAs in the metabolic processes of insects, particularly in relation to reproduction.".

Thanks for your wonderful suggestion. We have revised them in our revised manuscript, including deleted "present" in Line 383 and changed "More and more miRNAs have been reported to be involved in the metabolic processes of insects including reproduction" to "There is increasing evidence implicating miRNAs in the metabolic processes of insects, particularly in relation to reproduction" in Line 399-400.

(10) In line 423, change "After infection with C_Las, _D. citri are more fecund than their uninfected counterparts." to "Upon infection with C_Las, _D. citri exhibits enhanced fecundity compared to uninfected individuals.". In lines 424-425 and 439-440, change "the more offspring of D. citri, the more C_Las in the field" to "the increased offspring of _D. citri contributes to a higher presence of _C_Las in the field.". In Line 429, change " information" to "insights".

Thanks for your wonderful suggestion. We have revised them in our revised manuscript, including changed "After infection with C_Las, _D. citri are more fecund than their uninfected counterparts" to "Upon infection with C_Las, _D. citri exhibits enhanced fecundity compared to uninfected individuals" in Line 436-437; changed "the more offspring of D. citri, the more C_Las in the field" to "the increased offspring of _D. citri contributes to a higher presence of _C_Las in the field" in Line 438-439; changed "information" to "insights" in Line 443.

(11) In lines 446-447, change "The _C_Las-infected lemon plants and psyllids were monitored to detect _C_Las infection monthly using the quantitative polymerase chain reaction (qPCR)" to "Monthly monitoring of the _C_Las infection in both the lemon plants and psyllids was conducted using quantitative polymerase chain reaction (qPCR)".

Thanks for your wonderful suggestion. We have revised it in our revised manuscript (Line 460-461).

(12) In lines 452-458, how did the authors identify homologous sequences of AKH and AKHR for phylogenetic tree analysis and alignment of the amino acid sequences? From NCBI or other databases? The methodological details should be added.

Thanks for your wonderful suggestion. We have added the methodological details in our revised manuscript (Line 469-470).

(13) In line 476, Dcβ-ACT should be italic.

Thanks for your wonderful suggestion. We have changed “DcβACT” to italic in our revised manuscript (Line 491).

(14) In line 538, the manufacturer should be provided for Nile Red.

Thanks for your wonderful suggestion. We have provided the manufacturer of Nile Red in our revised manuscript (Line 553).

(15) Does miR-34 have any other target genes? If yes, whether they have any function in the fecundity improvement of D. citri after infected by CLas.

Thanks for your insightful suggestion. In addition to DcAKHR, we predicted three other genes have binding sites in 3’UTR with miR-34, including Innexin, T-box transcription factor TBX1, and fatty acid synthase. Despite this, the mRNA expression levels of all three genes remained unchanged between _C_Las-negative and _C_Las-postive females. Therefore, we believe that these genes are not implicated in the fecundity improvement.

(16) The reference format should be unified. Please revise references 10, 28, 43, 47, and 53.

Thanks for your wonderful suggestion. We have revised them in the revised manuscript.

Author response:

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

We thank the reviewers for their feedback on our manuscript. Taking the advice of the reviewers, we have streamlined the text and formatted the figures to conform to the format instructions. We believe that the revised manuscript has been improved. 

Point-by-point responses are presented below.

Reviewer #1:

(1) There is an over-interpretation regarding the results in Figure 6A. There is no difference between isoHD1 iMac control and HD1 Mut iMac.<br />

We thank the reviewer for his/her feedback on our manuscript. We have since changed the wordings on Page 11, line 294 of the manuscript, to reflect this important point.

Reviewer #2:

(2) The authors have not elucidated the significance of the increased CSF1 dosage in Figure 2F, aside from its effect on cell viability, lacking a thorough discussion of this result.

We have incorporated the significance of the results of our CSF1 dosage data with a newly added observation of an upregulated immature myeloid marker and downregulated expression mature macrophage marker within mutant iMac from the respective RNA-seq data (Page 5, line 163); and elaborated further within the Discussion section that this results in the possible generation of immature iMacs even after maturation (Page 14, line 356).

(3) Additionally, while transcriptomic and metabolic alterations related to the mutation were demonstrated in iMac models, similar investigations in iMicros are absent, necessitating further experiments to validate the findings across cell models.

We thank the reviewer for this feedback and feel that this is beyond the scope of this study at current stage, and that we would keep this in consideration to incorporate into subsequent experiments.

(4) The conclusion drawn regarding cytokine levels lacks robust support from the data, particularly considering the varied responses observed in different mutant lines. Further analysis of the secretome (e.g. via ELISA) could provide additional insights.

We thank the reviewer for this feedback and feel that this is beyond the scope of this study at current stage, and that we would keep this in consideration to incorporate into subsequent experiments.

(5) Moreover, the characterization of iMicros is incomplete, with limited protein-level analysis (e.g. validate RNA-seq via flow cytometry).

We thank the reviewer for this feedback and feel that this is beyond the scope of this study at current stage, and that we would keep this in consideration to incorporate into subsequent experiments.

(6) Additionally, the claim of microglial-like morphology lacks adequate evidence, as the provided image is insufficient for such an assessment.

We have added confocal images depicting microglial-like morphology in our co-culture system within Supp Fig 3C.

(7) RNA-seq experiments should be represented better, it is not possible to read the legends or gene names in the figures. Maybe the data sets can be combined into PCAone and one overall analysis, e.g. via WGCNA-like analyses? This would make it easier for the reader to compare the two cell lines side by side.

We have since enhanced the quality of the respective RNA-seq figures with enlarged data points and gene names for better clarity.

(8) Statistical test information is missing.

We are sorry for leaving this out and have added the statistical test information within Page 15 of the methods section.

(9) Finally, inconsistent terminology usage throughout the paper may confuse readers (iMac versus iMicros).

We have streamlined the terminology used within Page 10, line 265 and 267, of the manuscript for better consistency.

(10) Fig. 1D: which cell line is displayed here?

Mut HD1 iPSC is displayed here. We have also revised the figure legend of Fig 1D within Page 1, line 8 to include this information.

(11) Fig. 1E: Karyotype of which cell line is shown?

We have included karyotype of both IsoHD1 and IsoHD2 iPSC in Fig 1E, and also revised the legend within Page 1, line 11, to reflect this change.

(12) Supp. Fig. 1: scale bar information missing.

We thank the reviewer for pointing out this and have revised the legend within Page 1, line 17, to include scale bar information.

(13) Fig. 5: legend for A is missing.

We thank the reviewer for pointing out this and have revised the legend within Page 2, line 91, to include Figure (A) within.

14) Supp. Fig. 3A says 30 days, but only 23 days are shown.

We are sorry for making this inadvertent typo and have since aligned the correct days (31 days) shown within the figure (Supp Fig 3A) and legend (Page 3, line 110, 113), as mentioned in the manuscript.

(15) Supp. Fig. 3C: scale bar length is incorrect.

We did a recheck and are confident that the scale car is of the correct length. The images displaying the respective fluorescent channels are proportionately reduced with respect to the main figure (now Supp. Fig. 3D), and thus are of the same size (200 uM).

(16) Fig. 6: legend for D, E is missing.

We have revised the figure legend within Page 3, line 128, 130 and 131, to address said missing legends.

(17) Stem cells do also express Sox2. how does Sox2 expression lead to the conclusion of an optimal generated organoid?

We thank the reviewer for pointing this out. Sox2 has been defined as a core intrinsic factor for regulating pluripotency (Avilian et al, 2003, Zhang et al, 2014), as well as lineage specifiers to regulate ectodermal differentiation which is crucial in controlling neural initiation and differentiation from iPSC (Zhao et al, 2004, Thomson et al, 2011, Wang et al 2014). Additionally, Sox2 is highly expressed in proliferating neural progenitor cells as documented in previous iterations of cerebral organoids generation protocol (Lancaster et al 2013, Qian at el, 2018). Perhaps “optimally” sounds too forced in this context, as such we have toned down on the phrasing.  

(18) HD1 and HD2 react differently (e.g. in IL-1B production), but the text is written often as if both cell lines react in the same way.

We thank the reviewer for pointing this out and have since clarified this within Page 4, line 366-368, of the manuscript.

(19) Precise information on medium missing (e.g. no Pen/Strep?).

We thank the reviewer for pointing out this. Culturing of iPSC colonies was done without the use of Pen/Strep. Additionally, we have elaborated the medium composition for our iMac cultures for clarity within Page 4, line 106, of Materials and Methods as well as the information within Supp. Table 4.

(20) How was ReleSR used exactly?

We have included the usage of ReleSR within Page 2, line 41 of Materials and Methods.

(21) What kind of microscopes/objectives were used for imaging?

We have added the respective microscope details for bright-field, phase-contrast and cytospin related experiments within Page 3, line 73, and Page 14, line 360, of Materials and Methods.

(22) For the dissociation of organoids: what kind of pipit was use and at which temperature were organoids incubated?

We have included the pipette used for organoids dissociation, as well as the incubation temperature for organoids culture within Page 9, line 243, 244 and 245, of Materials and Methods.

(23) How was the RNA-seq analysis done? Which packages? Which versions?

We provide now the information requested in the material and method section.

Author response:

Response letter

Public Reviews:

Reviewer #1 (Public Review):

(1) It is a nice study but lacks some functional data required to determine how useful these alleles will be in practice, especially in comparison with the figure line that stimulated their creation.

We are grateful for this comment. For the usefulness of these alleles, figure 3 shows that specific and efficient genetic manipulation of one cell subpopulation can be achieved by mating across the DreER mouse strain to the rox-Cre mouse strain. In addition, figure 6 shows that R26-loxCre-tdT can effectively ensure Cre-loxP recombination on some gene alleles and for genetic manipulation. The expression of the tdT protein is aligned with the expression of the Cre protein (Alb roxCre-tdT and R26-loxCre-tdT, figure 2 and figure 5), which ensures the accuracy of the tracing experiments. We believe more functional data can be shown in future articles that use mice lines mentioned in this manuscript.

(2) The data in Figure 5 show strong activity at the Confetti locus, but the design of the newly reported R26-loxCre line lacks a WPRE sequence that was included in the iSure-Cre line to drive very robust protein expression.

Thank you for coming up with this point in the manuscript. In the R26-loxCre-tdT mice knock-in strategy, the WPRE sequence is added behind the loxCre-P2A-tdT sequence.

(3) the most valuable experiment for such a new tool would be a head-to-head comparison with iSure (or the latest iSure version from the Benedito lab) using the same CreER and target foxed allele. At the very least a comparison of Cre protein expression between the two lines using identical CreER activators is needed.

According to the reviewer’s suggestion, we will compare iSuRe-Cre with R26-loxCre-tdT by using Alb-CreER and target R26-Confetti in the revised manuscript.

(4) Why did the authors not use the same driver to compare mCre 1, 4, 7, and 10? The study in Figure 2 uses Alb-roxCre for 1 and 7 and Cdh5-roxCre for 4 and 10, with clearly different levels of activity driven by the two alleles in vivo. Thus whether mCre1 is really better than mCre4 or 10 is not clear.

Thank you for raising this concern. After screening out four robust versions of mCre, we generated these four roxCre knock-in mice. It is unpredictable for us which is the most robust mCre in vivo. It might be one or two mCre versions that work efficiently. For example, if Alb-mCre1 was competitive with Cdh5-mCre10, we can use them for targeting genes in different cell types, broadening the potential utility of these mice.

(5) Technical details are lacking. The authors provide little specific information regarding the precise way that the new alleles were generated, i.e. exactly what nucleotide sites were used and what the sequence of the introduced transgenes is. Such valuable information must be gleaned from schematic diagrams that are insufficient to fully explain the approach.

Thank you for your careful suggestions.

We will provide schematic figures as well as nucleotide sequences for mice generation in the revised manuscript.

Reviewer #2 (Public Review):

(1) The scenario where the lines would demonstrate their full potential compared to existing models has not been tested.

We are grateful for this suggestion. We will compare iSuRe-Cre with R26-loxCre-tdT by using Alb-CreER and target R26-Confetti in the revised manuscript.

(2) The challenge lies in performing such experiments, as low doses of tamoxifen needed for inducing mosaic gene deletion may not be sufficient to efficiently recombine multiple alleles in individual cells while at the same time accurately reporting gene deletion. Therefore, a demonstration of the efficient deletion of multiple floxed alleles in a mosaic fashion would be a valuable addition.

Thank you for your constructive comments. Mosaic analysis using sparse labeling and efficient gene deletion would be our future direction using roxCre and loxCre strategies. We will include some discussion of using such strategy in the revised manuscript.

(3) When combined with the confetti line, the reporter cassette will continue flipping, potentially leading to misleading lineage tracing results.

Thank you for your professional comments. Indeed, the confetti used in this study can continue flipping, which would lead to potentially misleading lineage tracing results. Our use of R26-Confetti is to demonstrate the robustness of mCre for recombination. Some multiple-color mice lines that don’t flip have been published, for example, R26-Confetti2(10.1038/s41588-019-0346-6) and Rainbow (10.1161/CIRCULATIONAHA.120.045750). These reporters could be used for tracing Cre-expressing cells, without concerns of flipping of reporter cassettes.

(4) Constitutive expression of Cre is also associated with toxicity, as discussed by the authors in the introduction.

Thank you for your professional comments. The toxicity of constitutive expression of Cre and the toxicity associated with tamoxifen treatment in CreER mice line (10.1038/s44161-022-00125-6) are known to the field. This study can’t solve the toxicity of the constitutive expression of Cre in this work. Many mouse lines with constitutive Cre driven by different promoters are present across various fields, representing similar toxicity. To solve this issue, it would be possible to construct a new strategy that enables the removal of Cre after its expression.

Reviewer #3 (Public Review):

(1) Although leakiness is rather minor according to the original publication and the senior author of the study wrote in a review a few years ago that there is no leakiness(https://doi.org/10.1016/j.jbc.2021.100509).

Thank you so much for your careful check. In this review (https://doi.org/10.1016/j.jbc. 2021.100509), the writer’s comments on iSuRe-Cre are on the reader's side, and all summary words are based on the original published paper (10.1038/s41467-019-10239-4). Currently, we have tested iSuRe-Cre in our hands. We did detect some leakiness in the heart and muscle, but hardly in other tissues as shown in the following figure.

Author response image 1.

Leakiness in Alb CreER;iSuRe-Cre mouse line. Pictures are representative results for 5 mice. Scale bars, white 100 µm.

(2) I would have preferred to see a study, which uses the wonderful new tools to address a major biological question, rather than a primarily technical report, which describes the ongoing efforts to further improve Cre and Dre recombinase-mediated recombination.

We gratefully appreciate your valuable comment. The roxCre and loxCre mice mentioned in this study provide more effective methods for inducible genetic manipulation in studying gene function. We hope that the application of our new genetic tools could help address some major biological questions in different biomedical fields in the future.

(3) Very high levels of Cre expression may cause toxic effects as previously reported for the hearts of Myh6-Cre mice. Thus, it seems sensible to test for unspecific toxic effects, which may be done by bulk RNA-seq analysis, cell viability, and cell proliferation assays. It should also be analyzed whether the combination of R26-roxCre-tdT with the Tnni3-Dre allele causes cardiac dysfunction, although such dysfunctions should be apparent from potential changes in gene expression.

We are sorry that we mistakenly spelled R26-loxCre-tdT into R26-roxCre-tdT in our manuscript. We have not generated R26-roxCre-tdT mouse line. We also thank the reviewer for concerns about the toxicity of high Cre expression. The toxicity of constitutive expression of Cre and the toxicity of tamoxifen treatment of CreER mice line (10.1038/s44161-022-00125-6) are known to the field. This study can’t solve the toxicity of the constitutive expression of Cre in this work. Many mouse lines with constitutive Cre driven by different promoters are present across various fields, representing similar toxicity. To solve this issue, it would be possible to construct a new strategy that enables the removal of Cre after its expression.

(4) Is there any leakiness when the inducible DreER allele is introduced but no tamoxifen treatment is applied? This should be documented. The same also applies to loxCre mice.

In this study, we come up with new mice tool lines, including Alb roxCre1-tdT, Cdh5 roxCre4-tdT, Alb roxCre7-GFP, Cdh5 roxCre10-GFP and R26-loxCre-tdT. As the data shown in supplementary figure 1, supplementary figure 2, and figure 4D, Alb roxCre1-tdT, Cdh5 roxCre4-tdT, Alb roxCre7-GFP, Cdh5 roxCre10-GFP and R26-loxCre-tdT are not leaky. Therefore, if there is any leakiness driven by the inducible DreER or CreER allele, the leakiness is derived from the DreER or CreER. We will supplement relevant experimental data in the revision.

(5) It would be very helpful to include a dose-response curve for determining the minimum dosage required in Alb-CreER; R26-loxCre-tdT; Ctnnb1flox/flox mice for efficient recombination.

Thank you for your suggestion. We understand the reviewer’s concern. We can do a dose-response curve in the revision work.

(6) In the liver panel of Figure 4F, tdT signals do not seem to colocalize with the VE-cad signals, which is odd. Is there any compelling explanation?

As the file-loading website has a file size limitation, the compressed image results in some signal unclear. The following are the zoom-out figures. The staining in Figure 4F will be optimized and high-resolution images will be provided in the revision.

Author response image 2.

(7) The authors claim that "virtually all tdT+ endothelial cells simultaneously expressed YFP/mCFP" (right panel of Figure 5D). Well, it seems that the abundance of tdT is much lower compared to YFP/mCFP. If the recombination of R26-Confetti was mainly triggered by R26-loxCre-tdT, the expression of tdT and YFP/mCFP should be comparable. This should be clarified.

Thank you so much for your careful check. We checked these signals carefully and didn't find the “much lower” tdT signal. As the file-loading website has a file size limitation, the compressed image results in some signal unclear. We attached clear high resolution images here. The following figure shows how we split the tdT signal and compared it with YFP/mCFP.

Author response image 3.

(8) In several cases, the authors seem to have mixed up "R26-roxCre-tdT" with "R26-loxCre-tdT". There are errors in #251 and #256.Furthermore, in the passage from line #278 to #301. In the lines #297 and #300 it should probably read "Alb-CreER; R26-loxCretdT;Ctnnb1flox/flox"" rather than "Alb-CreER;R26-tdT2;Ctnnb1flox/flox".

We are grateful for these careful observations. We have corrected these typos accordingly.

Author response:

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

Public Reviews:

Reviewer #1:

Summary:

The work by Combrisson and colleagues investigates the degree to which reward and punishment learning signals overlap in the human brain using intracranial EEG recordings. The authors used information theory approaches to show that local field potential signals in the anterior insula and the three sub regions of the prefrontal cortex encode both reward and punishment prediction errors, albeit to different degrees. Specifically, the authors found that all four regions have electrodes that can selectively encode either the reward or the punishment prediction errors. Additionally, the authors analyzed the neural dynamics across pairs of brain regions and found that the anterior insula to dorsolateral prefrontal cortex neural interactions were specific for punishment prediction errors whereas the ventromedial prefrontal cortex to lateral orbitofrontal cortex interactions were specific to reward prediction errors. This work contributes to the ongoing efforts in both systems neuroscience and learning theory by demonstrating how two differing behavioral signals can be differentiated to a greater extent by analyzing neural interactions between regions as opposed to studying neural signals within one region.

Strengths:

The experimental paradigm incorporates both a reward and punishment component that enables investigating both types of learning in the same group of subjects allowing direct comparisons.

The use of intracranial EEG signals provides much needed insight into the timing of when reward and punishment prediction errors signals emerge in the studied brain regions.

Information theory methods provide important insight into the interregional dynamics associated with reward and punishment learning and allows the authors to assess that reward versus punishment learning can be better dissociated based on interregional dynamics over local activity alone.

We thank the reviewer for this accurate summary. Please find below our answers to the weaknesses raised by the reviewer.

Weaknesses:

The analysis presented in the manuscript focuses solely on gamma band activity. The presence and potential relevance of other frequency bands is not discussed. It is possible that slow oscillations, which are thought to be important for coordinating neural activity across brain regions could provide additional insight.

We thank the reviewer for pointing us to this missing discussion in the first version of the manuscript. We now made this point clearer in the Methods sections entitled “iEEG data analysis” and “Estimate of single-trial gamma-band activity”:

“Here, we focused solely on broadband gamma for three main reasons. First, it has been shown that the gamma band activity correlates with both spiking activity and the BOLD fMRI signals (Lachaux et al., 2007; Mukamel et al., 2004; Niessing et al., 2005; Nir et al., 2007), and it is commonly used in MEG and iEEG studies to map task-related brain regions (Brovelli et al., 2005; Crone et al., 2006; Vidal et al., 2006; Ball et al., 2008; Jerbi et al., 2009; Darvas et al., 2010; Lachaux et al., 2012; Cheyne and Ferrari, 2013; Ko et al., 2013). Therefore, focusing on the gamma band facilitates linking our results with the fMRI and spiking literatures on probabilistic learning. Second, single-trial and time-resolved high-gamma activity can be exploited for the analysis of cortico-cortical interactions in humans using MEG and iEEG techniques (Brovelli et al., 2015; 2017; Combrisson et al., 2022). Finally, while previous analyses of the current dataset (Gueguen et al., 2021) reported an encoding of PE signals at different frequency bands, the power in lower frequency bands were shown to carry redundant information compared to the gamma band power.”

The data is averaged across all electrodes which could introduce biases if some subjects had many more electrodes than others. Controlling for this variation in electrode number across subjects would ensure that the results are not driven by a small subset of subjects with more electrodes.

We thank the reviewer for raising this important issue. We would like to point out that the gamma activity was not averaged across bipolar recordings within an area, nor measures of connectivity. Instead, we used a statistical approach proposed in a previous paper that combines non-parametric permutations with measures of information (Combrisson et al., 2022). As we explain in the “Statistical analysis” section, mutual information (MI) is estimated between PE signals and single-trial modulations in gamma activity separately for each contact (or for each pair of contacts). Then, a one-sample t-test is computed across all of the recordings of all subjects to form the effect size at the group-level. We will address the point of the electrode number in our answer below.

The potential variation in reward versus punishment learning across subjects is not included in the manuscript. While the time course of reward versus punishment prediction errors is symmetrical at the group level, it is possible that some subjects show faster learning for one versus the other type which can bias the group average. Subject level behavioral data along with subject level electrode numbers would provide more convincing evidence that the observed effects are not arising from these potential confounds.

We thank the reviewer for the two points raised. We performed additional analyses at the single-participant level to address the issues raised by the reviewer. We should note, however, that these results are descriptive and cannot be generalized to account for population-level effects. As suggested by the reviewer, we prepared two new figures. The first supplementary figure summarizes the number of participants that had iEEG contacts per brain region and pair of brain regions (Fig. S1A in the Appendix). It can be seen that the number of participants sampled in different brain regions is relatively constant (left panel) and the number of participants with pairs of contacts across brain regions is relatively homogeneous, ranging from 7 to 11 (right panel). Fig. S1B shows the number of bipolar derivations per subject and per brain region.

Author response image 1.

Single subject anatomical repartition. (A) Number of unique subject per brain region and per pair of brain regions (B) Number of bipolar derivations per subject and per brain region

The second supplementary figure describes the estimated prediction error for rewarding and punishing trials for each subject (Fig. S2). The single-subject error bars represent the 95th percentile confidence interval estimated using a bootstrap approach across the different pairs of stimuli presented during the three to six sessions. As the reviewer anticipated, there are indeed variations across subjects, but we observe that RPE and PPE are relatively symmetrical, even at the subject level, and tend toward zero around trial number 10. These results therefore corroborate the patterns observed at the group-level.

Author response image 2.

Single-subject estimation of predictions errors. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red), ± 95% confidence interval.

Finally, to assess the variability of local encoding of prediction errors across participants, we quantified the proportion of subjects having at least one significant bipolar derivation encoding either the RPE or PPE (Fig. S4). As expected, we found various proportions of unique subjects with significant R/PPE encoding per region. The lowest proportion was achieved in the ventromedial prefrontal cortex (vmPFC) and lateral orbitofrontal cortex (lOFC) for encoding PPE and RPE, respectively, with approximately 30% of the subjects having the effect. Conversely, we found highly reproducible encodings in the anterior insula (aINS) and dorsolateral prefrontal cortex (dlPFC) with a maximum of 100% of the 9 subjects having at least one bipolar derivation encoding PPE in the dlPFC.

Author response image 3.

Taken together, we acknowledge a certain variability per region and per condition. Nevertheless, the results presented in the supplementary figures suggest that the main results do not arise from a minority of subjects.

We would like to point out that in order to assess across-subject variability, a much larger number of participants would have been needed, given the low signal-to-noise ratios observed at the single-participant level. We thus prefer to add these results as supplementary material in the Appendix, rather than in the main text.

It is unclear if the findings in Figures 3 and 4 truly reflect the differential interregional dynamics in reward versus punishment learning or if these results arise as a statistical byproduct of the reward vs punishment bias observed within each region. For instance, the authors show that information transfer from anterior insula to dorsolateral prefrontal cortex is specific to punishment prediction error. However, both anterior insula and dorsolateral prefrontal cortex have higher prevalence of punishment prediction error selective electrodes to begin with. Therefore the findings in Fig 3 may simply be reflecting the prevalence of punishment specificity in these two regions above and beyond a punishment specific neural interaction between the two regions. Either mathematical or analytical evidence that assesses if the interaction effect is simply reflecting the local dynamics would be important to make this result convincing.

This is an important point that we partly addressed in the manuscript. More precisely, we investigated whether the synergistic effects observed between the dlPFC and vmPFC encoding global PEs (Fig. 5) could be explained by their respective local specificity. Indeed, since we reported larger proportions of recordings encoding the PPE in the dlPFC and the RPE in the vmPFC (Fig. 2B), we checked whether the synergy between dlPFC and vmPFC could be mainly due to complementary roles where the dlPFC brings information about the PPE only and the vmPFC brings information to the RPE only. To address this point, we selected PPE-specific bipolar derivations from the dlPFC and RPE-specific from the vmPFC and, as the reviewer predicted, we found synergistic II between the two regions probably mainly because of their respective specificity. In addition, we included the II estimated between non-selective bipolar derivations (i.e. recordings with significant encoding for both RPE and PPE) and we observed synergistic interactions (Fig. 5C and Fig. S9). Taken together, the local specificity certainly plays a role, but this is not the only factor in defining the type of interactions.

Concerning the interaction information results (II, Fig. 3), several lines of evidence suggest that local specificity cannot account alone for the II effects. For example, the local specificity for PPE is observed across all four areas (Fig. 2A) and the percentage of bipolar derivations displaying an effect is large (equal or above 10%) for three brain regions (aINS, dlPLF and lOFC). If the local specificity were the main driving cause, we would have observed significant redundancy between all pairs of brain regions. On the other hand, the interaction between the aINS and lOFC displayed no significant redundant effect (Fig. 3B). Another example is the result observed in lOFC: approximately 30% of bipolar derivations display a selectivity for PPE (Fig. 2B, third panel from the left), but do not show clear signs of redundant encoding at the level of within-area interactions (Fig. 3A, bottom-left panel). Similarly, the local encoding for RPE is observed across all four brain regions (Fig. 2A) and the percentage of bipolar derivations displaying an effect is large (equal or above 10%) for three brain regions (aINS, dlPLF and vmPFC). Nevertheless, significant between-regions interactions have been observed only between the lOFC and vmPFC (Fig. 3B bottom right panel).

To further support the reasoning, we performed a simulation to show that it is possible to observe synergistic interactions between two regions with the same specificity. As an example, we may consider one region locally encoding early trials of RPE and a second region encoding the late trials of the RPE. Combining the two with the II would lead to synergistic interactions, because each one of them carries information that is not carried by the other. To illustrate this point, we simulated the data of two regions (x and y). To simulate redundant interactions (first row), each region receives a copy of the prediction (one-to-all) and for the synergy (second row), x and y receive early and late PE trials, respectively (all-to-one). This toy example illustrates that the local specificity is not the only factor determining the type of their interactions. We added the following result to the Appendix.

Author response image 4.

Local specificity does not fully determine the type of interactions. Within-area local encoding of PE using the mutual information (MI, in bits) for regions X and Y and between-area interaction information (II, in bits) leading to (A) redundant interactions and (B) synergistic interactions about the PE

Regarding the information transfer results (Fig. 4), similar arguments hold and suggest that the prevalence is not the main factor explaining the arising transfer entropy between the anterior insula (aINS) and dorsolateral prefrontal cortex (dlPFC). Indeed, the lOFC has a strong local specificity for PPE, but the transfer entropy between the lOFC and aINS (or dlPFC) is shown in Fig. S7 does not show significant differences in encoding between PPE and RPE.

Indeed, such transfer can only be found when there is a delay between the gamma activity of the two regions. In this example, the transfer entropy quantifies the amount of information shared between the past activity of the aINS and the present activity of the dlPFC conditioned on the past activity of the dlPFC. The conditioning ensures that the present activity of the dlPFC is not only explained by its own past. Consequently, if both regions exhibit various prevalences toward reward and punishment but without delay (i.e. at the same timing), the transfer entropy would be null because of the conditioning. As a fact, between 10 to -20% of bipolar recordings show a selectivity to the reward PE (represented by a proportion of 40-60% of subjects, Fig.S4). However, the transfer entropy estimated from the aINS to the dlPFC across rewarding trials is flat and clearly non-significant. If the transfer entropy was a byproduct of the local specificity then we should observe an increase, which is not the case here.

Reviewer #2:

Summary:

Reward and punishment learning have long been seen as emerging from separate networks of frontal and subcortical areas, often studied separately. Nevertheless, both systems are complimentary and distributed representations of rewards and punishments have been repeatedly observed within multiple areas. This raised the unsolved question of the possible mechanisms by which both systems might interact, which this manuscript went after. The authors skillfully leveraged intracranial recordings in epileptic patients performing a probabilistic learning task combined with model-based information theoretical analyses of gamma activities to reveal that information about reward and punishment was not only distributed across multiple prefrontal and insular regions, but that each system showed specific redundant interactions. The reward subsystem was characterized by redundant interactions between orbitofrontal and ventromedial prefrontal cortex, while the punishment subsystem relied on insular and dorsolateral redundant interactions. Finally, the authors revealed a way by which the two systems might interact, through synergistic interaction between ventromedial and dorsolateral prefrontal cortex.

Strengths:

Here, the authors performed an excellent reanalysis of a unique dataset using innovative approaches, pushing our understanding on the interaction at play between prefrontal and insular cortex regions during learning. Importantly, the description of the methods and results is truly made accessible, making it an excellent resource to the community.

This manuscript goes beyond what is classically performed using intracranial EEG dataset, by not only reporting where a given information, like reward and punishment prediction errors, is represented but also by characterizing the functional interactions that might underlie such representations. The authors highlight the distributed nature of frontal cortex representations and propose new ways by which the information specifically flows between nodes. This work is well placed to unify our understanding of the complementarity and specificity of the reward and punishment learning systems.

We thank the reviewer for the positive feedback. Please find below our answers to the weaknesses raised by the reviewer.

Weaknesses:

The conclusions of this paper are mostly supported by the data, but whether the findings are entirely generalizable would require further information/analyses.

First, the authors found that prediction errors very quickly converge toward 0 (less than 10 trials) while subjects performed the task for sets of 96 trials. Considering all trials, and therefore having a non-uniform distribution of prediction errors, could potentially bias the various estimates the authors are extracting. Separating trials between learning (at the start of a set) and exploiting periods could prove that the observed functional interactions are specific to the learning stages, which would strengthen the results.

We thank the reviewer for this question. We would like to note that the probabilistic nature of the learning task does not allow a strict distinction between the exploration and exploitation phases. Indeed, the probability of obtaining the less rewarding outcome was 25% (i.e., for 0€ gain in the reward learning condition and -1€ loss in the punishment learning condition). Thus, participants tended to explore even during the last set of trials in each session. This is evident from the average learning curves shown in Fig. 1B of (Gueguen et al., 2021). Learning curves show rates of correct choice (75% chance of 1€ gain) in the reward condition (blue curves) and incorrect choice (75% chance of 1€ loss) in the punishment condition (red curves).

For what concerns the evolution of PEs, as reviewer #1 suggested, we added a new figure representing the single-subject estimates of the R/PPE (Fig S2). Here, the confidence interval is obtained across all pairs of stimuli presented during the different sessions. We retrieved the general trend of the R/PPE converging toward zero around 10 trials. Both average reward and punishment prediction errors converge toward zero in approximately 10 trials, single-participant curves display large variability, also at the end of each session. As a reminder, the 96 trials represent the total number of trials for one session for the four pairs and the number of trials for each stimulus was only 24.

Author response image 5.

Single-subject estimation of predictions errors. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red), ± 95% confidence interval

However, the convergence of the R/PPE is due to the average across the pairs of stimuli. In the figure below, we superimposed the estimated R/PPE, per pair of stimuli, for each subject. It becomes very clear that high values of PE can be reached, even for late trials. Therefore, we believe that the split into early/late trials because of the convergence of PE is far from being trivial.

Author response image 6.

Single-subject estimation of predictions errors per pair of stimuli. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red)

Consequently, nonzero PRE and PPE occur during the whole session and separating trials between learning (at the start of a set) and exploiting periods, as suggested by the reviewer, does not allow a strict dissociation between learning vs no-learning. Nevertheless, we tested the analysis proposed by the reviewer, at the local level. We splitted the 24 trials of each pair of stimuli into early, middle and late trials (8 trials each). We then reproduced Fig. 2 by computing the mutual information between the gamma activity and the R/PPE for subsets of trials: early (first row) and late trials (second row). We retrieved significant encoding of both R/PPE in the aINS, dlPFC and lOFC in both early and late trials. The vmPFC also showed significant encoding of both during early trials. The only difference emerges in the late trials of the vmPFC where we found a strong encoding of the RPE only. It should also be noted that here since we are sub-selecting the trials, the statistical analyses are only performed using a third of the trials.

Taken together, the combination of high values of PE achieved even for late trials and the fact that most of the findings are reproduced even with a third of the trials does not justify the split into early and late trials here. Crucially, this latest analysis confirms that the neural correlates of learning that we observed reflect PE signals rather than early versus late trials in the session.

Author response image 7.

MI between gamma activity and R/PPE using early and late trials. Time courses of MI estimated between the gamma power and both RPE (blue) and PPE (red) using either early or late trials (first and second row, respectively). Horizontal thick lines represent significant clusters of information (p<0.05, cluster-based correction, non-parametric randomization across epochs).

Importantly, it is unclear whether the results described are a common feature observed across subjects or the results of a minority of them. The authors should report and assess the reliability of each result across subjects. For example, the authors found RPE-specific interactions between vmPFC and lOFC, even though less than 10% of sites represent RPE or both RPE/PPE in lOFC. It is questionable whether such a low proportion of sites might come from different subjects, and therefore whether the interactions observed are truly observed in multiple subjects. The nature of the dataset obviously precludes from requiring all subjects to show all effects (given the known limits inherent to intracerebral recording in patients), but it should be proven that the effects were reproducibly seen across multiple subjects.

We thank the reviewer for this remark that has also been raised by the first reviewer. This issue was raised by the first reviewer. Indeed, we added a supplementary figure describing the number of unique subjects per brain region and per pair of brain regions (Fig. S1A) such as the number of bipolar derivations per region and per subject (Fig. S1B).

Author response image 8.

Single subject anatomical repartition. (A) Number of unique subject per brain region and per pair of brain regions (B) Number of bipolar derivations per subject and per brain region

Regarding the reproducibility of the results across subjects for the local analysis (Fig. 2), we also added the instantaneous proportion of subjects having at least one bipolar derivation showing a significant encoding of the RPE and PPE (Fig. S4). We found a minimum proportion of approximately 30% of unique subjects having the effect in the lOFC and vmPFC, respectively with the RPE and PPE. On the other hand, both the aINS and dlPFC showed between 50 to 100% of the subjects having the effect. Therefore, local encoding of RPE and PPE was never represented by a single subject.

Author response image 9.

Similarly, we performed statistical analysis on interaction information at the single-subject level and counted the proportion of unique subjects having at least one pair of recordings with significant redundant and synergistic interactions about the RPE and PPE (Fig. S5). Consistently with the results shown in Fig. 3, the proportions of significant redundant and synergistic interactions are negative and positive, respectively. For the within-regions interactions, approximately 60% of the subjects with redundant interactions are about R/PPE in the aINS and about the PPE in the dlPFC and 40% about the RPE in the vmPFC. For the across-regions interactions, 60% of the subjects have redundant interactions between the aINS-dlPFC and dlPFC-lOFC about the PPE, and 30% have redundant interactions between lOFC-vmPFC about the RPE. Globally, we reproduced the main results shown in Fig. 3.

Author response image 10.

Inter-subjects reproducibility of redundant interactions about PE signals. Time-courses of proportion of subjects having at least one pair of bipolar derivation with a significant interaction information (p<0.05, cluster-based correction, non-parametric randomization across epochs) about the RPE (blue) or PPE (red). Data are aligned to the outcome presentation (vertical line at 0 seconds). Proportion of subjects with redundant (solid) and synergistic (dashed) interactions are respectively going downward and upward.

Finally, the timings of the observed interactions between areas preclude one of the authors' main conclusions. Specifically, the authors repeatedly concluded that the encoding of RPE/PPE signals are "emerging" from redundancy-dominated prefrontal-insular interactions. However, the between-region information and transfer entropy between vmPFC and lOFC for example is observed almost 500ms after the encoding of RPE/PPE in these regions, questioning how it could possibly lead to the encoding of RPE/PPE. It is also noteworthy that the two information measures, interaction information and transfer entropy, between these areas happened at non overlapping time windows, questioning the underlying mechanism of the communication at play (see Figures 3/4). As an aside, when assessing the direction of information flow, the authors also found delays between pairs of signals peaking at 176ms, far beyond what would be expected for direct communication between nodes. Discussing this aspect might also be of importance as it raises the possibility of third-party involvement.

The local encoding of RPE in the vmPFC and lOFC is observed in a time interval ranging from approximately 0.2-0.4s to 1.2-1.4s after outcome presentation (blue bars in Fig. 2A). The encoding of RPE by interaction information covers a time interval from approximately 1.1s to 1.5s (blue bars in Fig. 3B, bottom right panel). Similarly, significant TE modulations between the vmPFC and lOFC specific for PPE occur mainly in the 0.7s-1.1s range. Thus, it seems that the local encoding of PPE precedes the effects observed at the level of the neural interactions (II and TE). On the other hand, the modulations in MI, II and TE related to PPE co-occur in a time window from 0.2s to 0.7s after outcome presentation. Thus, we agree with the reviewer that a generic conclusion about the potential mechanisms relating the three levels of analysis cannot be drawn. We thus replaced the term “emerge from” by “occur with” from the manuscript which may be misinterpreted as hinting at a potential mechanism. We nevertheless concluded that the three levels of analysis (and phenomena) co-occur in time, thus hinting at a potential across-scales interaction that needs further study. Indeed, our study suggests that further work, beyond the scope of the current study, is required to better understand the interaction between scales.

Regarding the delay for the conditioning of the transfer entropy, the value of 176 ms reflects the delay at which we observed a maximum of transfer entropy. However, we did not use a single delay for conditioning, we used every possible delay between [116, 236] ms, as explained in the Method section. We would like to stress that transfer entropy is a directed metric of functional connectivity, and it can only be interpreted as quantifying statistical causality defined in terms of predictacìbility according to the Wiener-Granger principle, as detailed in the methods. Thus, it cannot be interpreted in Pearl’s causal terms and as indexing any type of direct communication between nodes. This is a known limitation of the method, which has been stressed in past literature and that we believe does not need to be addressed here.

To account for this, we revised the discussion to make sure this issue is addressed in the following paragraph:

“Here, we quantified directional relationships between regions using the transfer entropy (Schreiber, 2000), which is a functional connectivity measure based on the Granger-Wiener causality principle. Tract tracing studies in the macaque have revealed strong interconnections between the lOFC and vmPFC in the macaque (Carmichael and Price, 1996; Öngür and Price, 2000). In humans, cortico-cortical anatomical connections have mainly been investigated using diffusion magnetic resonance imaging (dMRI). Several studies found strong probabilities of structural connectivity between the anterior insula with the orbitofrontal cortex and dorsolateral part of the prefrontal cortex (Cloutman et al., 2012; Ghaziri et al., 2017), and between the lOFC and vmPFC (Heather Hsu et al., 2020). In addition, the statistical dependency (e.g. coherence) between the LFP of distant areas could be potentially explained by direct anatomical connections (Schneider et al., 2021; Vinck et al., 2023). Taken together, the existence of an information transfer might rely on both direct or indirect structural connectivity. However, here we also reported differences of TE between rewarding and punishing trials given the same backbone anatomical connectivity (Fig. 4). [...] “

Reviewer #3:

Summary:

The authors investigated that learning processes relied on distinct reward or punishment outcomes in probabilistic instrumental learning tasks were involved in functional interactions of two different cortico-cortical gamma-band modulations, suggesting that learning signals like reward or punishment prediction errors can be processed by two dominated interactions, such as areas lOFC-vmPFC and areas aINS-dlPFC, and later on integrated together in support of switching conditions between reward and punishment learning. By performing the well-known analyses of mutual information, interaction information, and transfer entropy, the conclusion was accomplished by identifying directional task information flow between redundancy-dominated and synergy-dominated interactions. Also, this integral concept provided a unifying view to explain how functional distributed reward and/or punishment information were segregated and integrated across cortical areas.

Strengths:

The dataset used in this manuscript may come from previously published works (Gueguen et al., 2021) or from the same grant project due to the methods. Previous works have shown strong evidence about why gamma-band activities and those 4 areas are important. For further analyses, the current manuscript moved the ideas forward to examine how reward/punishment information transfer between recorded areas corresponding to the task conditions. The standard measurements such mutual information, interaction information, and transfer entropy showed time-series activities in the millisecond level and allowed us to learn the directional information flow during a certain window. In addition, the diagram in Figure 6 summarized the results and proposed an integral concept with functional heterogeneities in cortical areas. These findings in this manuscript will support the ideas from human fMRI studies and add a new insight to electrophysiological studies with the non-human primates.

We thank the reviewer for the summary such as for highlighting the strengths. Please find below our answers regarding the weaknesses of the manuscript.

Weaknesses:

After reading through the manuscript, the term "non-selective" in the abstract confused me and I did not actually know what it meant and how it fits the conclusion. If I learned the methods correctly, the 4 areas were studied in this manuscript because of their selective responses to the RPE and PPE signals (Figure 2). The redundancy- and synergy-dominated subsystems indicated that two areas shared similar and complementary information, respectively, due to the negative and positive value of interaction information (Page 6). For me, it doesn't mean they are "non-selective", especially in redundancy-dominated subsystem. I may miss something about how you calculate the mutual information or interaction information. Could you elaborate this and explain what the "non-selective" means?

In the study performed by Gueguen et al. in 2021, the authors used a general linear model (GLM) to link the gamma activity to both the reward and punishment prediction errors and they looked for differences between the two conditions. Here, we reproduced this analysis except that we used measures from the information theory (mutual information) that were able to capture linear and non-linear relationships (although monotonic) between the gamma activity and the prediction errors. The clusters we reported reflect significant encoding of either the RPE and/or the PPE. From Fig. 2, it can be seen that the four regions have a gamma activity that is modulated according to both reward and punishment PE. We used the term “non-selective”, because the regions did not encode either one or the other, but various proportions of bipolar derivations encoding either one or both of them.

The directional information flows identified in this manuscript were evidenced by the recording contacts of iEEG with levels of concurrent neural activities to the task conditions. However, are the conclusions well supported by the anatomical connections? Is it possible that the information was transferred to the target via another area? These questions may remain to be elucidated by using other approaches or animal models. It would be great to point this out here for further investigation.

We thank the reviewer for this interesting question. We added the following paragraph to the discussion to clarify the current limitations of the transfer entropy and the link with anatomical connections :

“Here, we quantified directional relationships between regions using the transfer entropy (Schreiber, 2000), which is a functional connectivity measure based on the Granger-Wiener causality principle. Tract tracing studies in the macaque have revealed strong interconnections between the lOFC and vmPFC in the macaque (Carmichael and Price, 1996; Öngür and Price, 2000). In humans, cortico-cortical anatomical connections have mainly been investigated using diffusion magnetic resonance imaging (dMRI). Several studies found strong probabilities of structural connectivity between the anterior insula with the orbitofrontal cortex and dorsolateral part of the prefrontal cortex (Cloutman et al., 2012; Ghaziri et al., 2017), and between the lOFC and vmPFC (Heather Hsu et al., 2020). In addition, the statistical dependency (e.g. coherence) between the LFP of distant areas could be potentially explained by direct anatomical connections (Schneider et al., 2021). Taken together, the existence of an information transfer might rely on both direct or indirect structural connectivity. However, here we also reported differences of TE between rewarding and punishing trials given the same backbone anatomical connectivity (Fig. 4). Our results are further supported by a recent study involving drug-resistant epileptic patients with resected insula who showed poorer performance than healthy controls in case of risky loss compared to risky gains (Von Siebenthal et al., 2017).”

References

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Cloutman LL, Binney RJ, Drakesmith M, Parker GJM, Lambon Ralph MA. 2012. The variation of function across the human insula mirrors its patterns of structural connectivity: Evidence from in vivo probabilistic tractography. NeuroImage 59:3514–3521. oi:10.1016/j.neuroimage.2011.11.016

Combrisson E, Allegra M, Basanisi R, Ince RAA, Giordano BL, Bastin J, Brovelli A. 2022. Group-level inference of information-based measures for the analyses of cognitive brain networks from neurophysiological data. NeuroImage 258:119347. doi:10.1016/j.neuroimage.2022.119347

Ghaziri J, Tucholka A, Girard G, Houde J-C, Boucher O, Gilbert G, Descoteaux M, Lippé S, Rainville P, Nguyen DK. 2017. The Corticocortical Structural Connectivity of the Human Insula. Cereb Cortex 27:1216–1228. doi:10.1093/cercor/bhv308

Gueguen MCM, Lopez-Persem A, Billeke P, Lachaux J-P, Rheims S, Kahane P, Minotti L, David O, Pessiglione M, Bastin J. 2021. Anatomical dissociation of intracerebral signals for reward and punishment prediction errors in humans. Nat Commun 12:3344. doi:10.1038/s41467-021-23704-w

Heather Hsu C-C, Rolls ET, Huang C-C, Chong ST, Zac Lo C-Y, Feng J, Lin C-P. 2020. Connections of the Human Orbitofrontal Cortex and Inferior Frontal Gyrus. Cereb Cortex 30:5830–5843. doi:10.1093/cercor/bhaa160

Lachaux J-P, Fonlupt P, Kahane P, Minotti L, Hoffmann D, Bertrand O, Baciu M. 2007. Relationship between task-related gamma oscillations and BOLD signal: new insights from combined fMRI and intracranial EEG. Hum Brain Mapp 28:1368–1375. doi:10.1002/hbm.20352

Mukamel R, Gelbard H, Arieli A, Hasson U, Fried I, Malach R. 2004. Coupling Between Neuronal Firing, Field Potentials, and fMRI in Human Auditory Cortex. Cereb Cortex 14:881.

Niessing J, Ebisch B, Schmidt KE, Niessing M, Singer W, Galuske RA. 2005. Hemodynamic signals correlate tightly with synchronized gamma oscillations. science 309:948–951.

Nir Y, Fisch L, Mukamel R, Gelbard-Sagiv H, Arieli A, Fried I, Malach R. 2007. Coupling between neuronal firing rate, gamma LFP, and BOLD fMRI is related to interneuronal correlations. Curr Biol 17:1275–1285.

Öngür D, Price JL. 2000. The organization of networks within the orbital and medial prefrontal cortex of rats, monkeys and humans. Cereb Cortex 10:206–219.

Schneider M, Broggini AC, Dann B, Tzanou A, Uran C, Sheshadri S, Scherberger H, Vinck M. 2021. A mechanism for inter-areal coherence through communication based on connectivity and oscillatory power. Neuron 109:4050-4067.e12. doi:10.1016/j.neuron.2021.09.037

Schreiber T. 2000. Measuring information transfer. Phys Rev Lett 85:461.

Von Siebenthal Z, Boucher O, Rouleau I, Lassonde M, Lepore F, Nguyen DK. 2017. Decision-making impairments following insular and medial temporal lobe resection for drug-resistant epilepsy. Soc Cogn Affect Neurosci 12:128–137. doi:10.1093/scan/nsw152

Recommendations for the authors

Reviewer #1

(1) Overall, the writing of the manuscript is dense and makes it hard to follow the scientific logic and appreciate the key findings of the manuscript. I believe the manuscript would be accessible to a broader audience if the authors improved the writing and provided greater detail for their scientific questions, choice of analysis, and an explanation of their results in simpler terms.

We extensively modified the introduction to better describe the rationale and research question.

(2) In the introduction the authors state "we hypothesized that reward and punishment learning arise from complementary neural interactions between frontal cortex regions". This stated hypothesis arrives rather abruptly after a summary of the literature given that the literature summary does not directly inform their stated hypothesis. Put differently, the authors should explicitly state what the contradictions and/or gaps in the literature are, and what specific combinations of findings guide them to their hypothesis. When the authors state their hypothesis the reader is still left asking: why are the authors focusing on the frontal regions? What do the authors mean by complementary interactions? What specific evidence or contradiction in the literature led them to hypothesize that complementary interactions between frontal regions underlie reward and punishment learning?

We extensively modified the introduction and provided a clearer description of the brain circuits involved and the rationale for searching redundant and synergistic interactions between areas.

(3) Related to the above point: when the authors subsequently state "we tested whether redundancy- or synergy dominated interactions allow the emergence of collective brain networks differentially supporting reward and punishment learning", the Introduction (up to the point of this sentence) has not been written to explain the synergy vs. redundancy framework in the literature and how this framework comes into play to inform the authors' hypothesis on reward and punishment learning.

We extensively modified the introduction and provided a clearer description of redundant and synergistic interactions between areas.

(4) The explanation of redundancy vs synergy dominated brain networks itself is written densely and hard to follow. Furthermore, how this framework informs the question on the neural substrates of reward versus punishment learning is unclear. The authors should provide more precise statements on how and why redundancy vs. synergy comes into play in reward and punishment learning. Put differently, this redundancy vs. synergy framework is key for understanding the manuscript and the introduction is not written clearly enough to explain the framework and how it informs the authors' hypothesis and research questions on the neural substrates of reward vs. punishment learning.

Same as above

(5) While the choice of these four brain regions in context of reward and punishment learning does makes sense, the authors do not outline a clear scientific justification as to why these regions were selected in relation to their question.

Same as above

(6) Could the authors explain why they used gamma band power (as opposed to or in addition to the lower frequency bands) to investigate MI. Relatedly, when the authors introduce MI analysis, it would be helpful to briefly explain what this analysis measures and why it is relevant to address the question they are asking.

Please see our answer to the first public comment. We added a paragraph to the discussion section to justify our choice of focusing on the gamma band only. We added the following sentence to the result section to justify our choice for using mutual-information:

The MI allowed us to detect both linear and non-linear relationships between the gamma activity and the PE

An extended explanation justifying our choice for the MI was already present in the method section.

(7) The authors state that "all regions displayed a local "probabilistic" encoding of prediction errors with temporal dynamics peaking around 500 ms after outcome presentation". It would be helpful for the reader if the authors spelled out what they mean by probabilistic in this context as the term can be interpreted in many different ways.

We agree with the reviewer that the term “probabilistic” can be interpreted in different ways. In the revised manuscript we changed “probabilistic” for “mixed”.

(8) The authors should include a brief description of how they compute RPE and PPE in the beginning of the relevant results section.

The explanation of how we estimated the PE is already present in the result section: “We estimated trial-wise prediction errors by fitting a Q-learning model to behavioral data. Fitting the model consisted in adjusting the constant parameters to maximize the likelihood of observed choices etc.”

(9) It is unclear from the Methods whether the authors have taken any measures to address the likely difference in the number of electrodes across subjects. For example, it is likely that some subjects have 10 electrodes in vmPFC while others may have 20. In group analyses, if the data is simply averaged across all electrodes then each subject contributes a different number of data points to the analysis. Hence, a subject with more electrodes can bias the group average. A starting point would be to state the variation in number of electrodes across subjects per brain region. If this variation is rather small, then simple averaging across electrodes might be justified. If the variation is large then one idea would be to average data across electrodes within subjects prior to taking the group average or use a resampling approach where the minimum number of electrodes per brain area is subsampled.

We addressed this point in our public answers. As a reminder, the new version of the manuscript contains a figure showing the number of unique patients per region, the PE at per participant level together with local-encoding at the single participant level.

(10) One thing to consider is whether the reward and punishment in the task is symmetrical in valence. While 1$ increase and 1$ decrease is equivalent in magnitude, the psychological effect of the positive (vs. the negative) outcome may still be asymmetrical and the direction and magnitude of this asymmetry can vary across individuals. For instance, some subjects may be more sensitive to the reward (over punishment) while others are more sensitive to the punishment (over reward). In this scenario, it is possible that the differentiation observed in PPE versus RPE signals may arise from such psychological asymmetry rather than the intrinsic differences in how certain brain regions (and their interactions) may encode for reward vs punishment. Perhaps the authors can comment on this possibility, and/or conduct more in depth behavioral analysis to determine if certain subjects adjust their choice behavior faster in response to reward vs. punishment contexts.

While it could be possible that individuals display different sensitivities vis-à-vis positive and negative prediction errors (and, indeed, a vast body of human reinforcement learning literature seems to point in this direction; Palminteri & Lebreton, 2022), it is unclear to us how such differences would explain into the recruitment of anatomically distinct areas reward and punishment prediction errors. It is important to note here that our design partially orthogonalized positive and reward vs. negative and punishment PEs, because the neutral outcome can generate both positive and negative prediction errors, as a function of the learning context (reward-seeking and punishment avoidance). Back to the main question, for instance, Lefebvre et al (2017) investigated with fMRI the neural correlates of reward prediction errors only and found that inter-individual differences in learning rates for positive and negative prediction errors correlated with differences in the degree of striatal activation and not with the recruitment of different areas. To sum up, while we acknowledge that individuals may display different sensitivity to prediction errors (and reward magnitudes), we believe that such differences should translated in difference in the degree of activation of a given system (the reward systems vs the punishment one) rather than difference in neural system recruitment

(11) As summarized in Fig 6, the authors show that information transfer between aINS to dlPFC was PPE specific whereas the information transfer between vmPFC to lOFC was RPE specific. What is unclear is if these findings arise as an inevitable statistical byproduct of the fact that aINS has high PPE-specificity and that vmPFC has high RPE-specificity. In other words, it is possible that the analysis in Fig 3,4 are sensitive to fact that there is a larger proportion of electrodes with either PPE or RPE sensitivity in aINS and vmPFC respectively - and as such, the II analysis might reflect the dominant local encoding properties above and beyond reflecting the interactions between regions per se. Simply put, could the analysis in Fig 3B turn out in any other way given that there are more PPE specific electrodes in aINS and more RPE specific electrodes in vmPFC? Some options to address this question would be to limit the electrodes included in the analyses (in Fig 3B for example) so that each region has the same number of PPE and RPE specific electrodes included.

Please see the simulation we added to the revised manuscript (Fig. S10) demonstrating that synergistic interactions can emerge between regions with the same specificity.

Regarding the possibility that Fig. 3 and 4 are sensitive to the number of bipolar derivations being R/PPE specific, a counter-example is the vmPFC. The vmPFC has a few recordings specific to punishment (Fig. 2) in almost 30% of the subjects (Fig. S4). However, there is no II about the PPE between recordings of the vmPFC (Fig. 3). The same reasoning also holds for the lOFC. Therefore, the proportion of recordings being RPE or PPE-specific is not sufficient to determine the type of interactions.

(12)  Related to the point above, what would the results presented in Fig 3A (and 3B) look like if the authors ran the analyses on RPE specific and PPE specific electrodes only. Is the vmPFC-vmPFC RPE effect in Fig 3A arising simply due to the high prevalence of RPE specific electrodes in vmPFC (as shown in Fig. 2)?

Please see our answer above.

Reviewer #2:

Regarding Figure 2A, the authors argued that their findings "globally reproduced their previously published findings" (from Gueguen et al, 2021). It is worth noting though that in their original analysis, both aINS and lOFC show differential effects (aINS showing greater punishment compared to reward, and the opposite for lOFC) compared to the current analysis. Although I would be akin to believe that the nonlinear approach used here might explain part of the differences (as the authors discussed), I am very wary of the other argument advanced: "the removal of iEEG sites contaminated with pathological activity". This raised some red flags. Does that mean some of the conclusions observed in Gueguen et al (2021) are only the result of noise contamination, and therefore should be disregarded? The author might want to add a short supplementary figure using the same approach as in Gueguen (2021) but using the subset of contacts used here to comfort potential readers of the validity of their previous manuscript.

We appreciate the reviewer's concerns and understand the request for additional information. However, we would like to point out that the figure suggested by the reviewer is already present in the supplementary files of Gueguen et al. 2021 (see Fig. S2). The results of this study should not be disregarded, as the supplementary figure reproduces the results of the main text after excluding sites with pathological activity. Including or excluding sites contaminated with epileptic activity does not have a significant impact on the results, as analyses are performed at each time-stamp and across trials, and epileptic spikes are never aligned in time across trials.

That being said, there are some methodological differences between the two studies. To extract gamma power, Gueguen et al. filtered and averaged 10 Hz sub-bands, while we used multi-tapers. Additionally, they used a temporal smoothing of 250 ms, while we used less smoothing. However, as explained in the main text, we used information-theoretical approaches to capture the statistical dependencies between gamma power and PE. Despite divergent methodologies, we obtained almost identical results.

The data and code supporting this manuscript should be made available. If raw data cannot be shared for ethical reasons, single-trial gamma activities should at least be provided. Regarding the code used to process the data, sharing it could increase the appeal (and use) of the methods applied.

We thank the reviewer for this suggestion. We added a section entitled “Code and data availability” and gave links to the scripts, notebooks and preprocessed data.

Author response:

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

We greatly appreciate the recommendations of the reviewers and have performed further analyses with existing data where requested. 

Below are our responses to each of the individual points. 

Reviewer #1 (Recommendations For The Authors):

(1) P11 mouse retina is still quite young, would MG isolated from adult retina be more interesting and relevant to disease-oriented cell replacement therapy? How efficiently would the sci-Plex system work for in vitro screen of mature murine MG?

Thank you for bringing this up. While a protocol for the conversion of MG to neurons with adult mice in vivo exists, it has proven to be more difficult to maintain adult MG in dissociated cell cultures, due to their more limited proliferation in vitro. This makes it difficult to use the sci-Plex assay, since cell number is limiting for treatment conditions. Therefore, we have chosen the strategy of screening on P11, where MG undergo proliferative cell divisions in dissociated cultures, allowing us to grow the millions of cells needed for this assay, and then to test the efficacy of the compounds we find from the screen with an adult in vivo assay.

(2) The study identified and tested the compounds individually, how would a combination of the compounds work in vivo? It would be interesting to examine how different combinations may affect the reprogramming efficiency and neuronal compositions.

We agree that this would be very interesting to investigate.  However, the number of treatment conditions then expands beyond the scale of the current sci-Plex technology with the number of MG that we are able to collect.  We instead adopted the strategy of casting a very wide net to identify additional molecular pathways that might be important in the reprogramming process.

(3) In-depth mechanistic and/or functional studies of the reprogrammed MG are highly desirable to improve the quality and significance of the study and to better understand how the compounds may influence the signaling and the reprogramming process.

While we agree that this would strengthen the study, this would increase the scope of the required revisions considerably. We are very interested in following up on some of the hits and look forward to providing additional details of mechanisms in future publications.  However, we feel that reporting this method and the results will stimulate those interested in reprogramming glia in other areas of the nervous system to test the compounds we identified in this assay.

Reviewer #2 (Recommendations For The Authors):

(1) The authors employed two protocols to initiate direct reprogramming of MG into retinal neurons in vitro. These protocols, referred to as "Timecourse" and "Pulse," involved short-term treatments lasting no more than 5 days. However, the findings obtained indicate that these brief treatments were insufficient to achieve a stable conversion. This conclusion is supported by the comparison between the "4 days (Timecourse)" and "4 days (Pulse)" conditions, as depicted in Figure 1 (D and E). In this set of experiments, labeling cells that express specific neuronal markers as neurons raises concerns, as these cells may have multiple fates, either died, reverted, arrested in certain intermediate stages, or converted to functional neurons. It is thus critical to determine whether the conversion to functional neurons is enhanced.

We thank you for your concern about this. We aimed to be very careful in our naming. In our naming scheme for this figure, we only consider the small number of cells with specific Bipolar markers (Trpm1, Grm6, Capb5, Otx2) neurons based on previous publications ((Jorstad et al. 2017; Todd et al. 2021; Todd et al. 2022; Todd et al. 2020)). The other cells that have some neuronal markers are identified as neuronal precursors (NeuPre) and are, as you mentioned, not necessarily mature/functional. While these NeuPre cells may eventually have multiple fates/may die/may revert to more ProL cells at some rate we believe it’s fair to define them as Neuronal Precursors due to the genes they are expressing (Dcx, Snap25, Elavl3, Gap43) at the moment of collection.  

Furthermore, your statement indicating that “the findings obtained indicate that these brief treatments were insufficient to achieve a stable conversion” is not what we intended to demonstrate. The text will be reworked to reflect what we hoped to convey. We acknowledge that 1) the majority cells are not stably converted, and 2) the levels of NeuPre cells are lower in the Pulse experiment overall, but this is true even at Day 5 when the conditions should be the same across experiments. The Pulse and Timecourse experiments were done on different days, and having previously found that there are differences in MG to BP conversion rate from experiment to experiment, these results were not unexpected. Of more note to us was that while ProL cells, Transition cells, and MG have very different patterns of abundance across time when comparing the experiments, the NeuPre cells accumulate at a similar time and pattern across the two experiments. This indicated to us that they uniquely have some amount of Ascl1 independent stability in their cell fate even when exposed to Ascl1 for as little as 3 days. See Author response image 1 below. This plot will be added to Fig. S1.

Author response image 1.

(2) The authors made a claim that a pseudo time value of 15 represents a crucial timepoint where the transition in cell fate becomes stable and ceases to rely on ectopic Ascl1 expression. However, it is essential to provide concrete evidence to substantiate this assertion. It is prudent to perform quantitative analyses rather than relying solely on the deduced trajectory to make this claim.

This is a fair point, the value of 15 was estimated by eye. We have returned to the data and estimated a density function for the pseudotime scores of the cells from the 1, 2, 3, and 4 day conditions in both the Pulse and Timecourse experiments (Author response image 2A-B below). We then calculated 16 to be the local minima between the pseudotime values of 10-20 for the Pulse experiment (Blue line). When comparing the two experiments, it’s apparent that there is a massive accumulation of cells with a pseudotime value just lower than 16 in the Timecouse experiment (values 10-15), and very few cells across the same region for the Pulse experiment, indicating some dependence on continued Ascl1 expression for the cell fate that exists from pseudotime 10-16 (mostly ProL cells). To the contrary, cells with greater pseudotime values exist across both experiments at similar levels.

We have also looked at the expression of Ascl1 along the pseudotime trajectory in the Timecourse experiment. Interestingly, and consistent with experiments in previous studies, both in vitro and in vivo (Todd et al. 2021; Todd et al. 2022; Todd et al. 2020), we see a decrease in Ascl1 expression as the cells move towards the end of the pseudotime trajectory (C below). It’s intriguing to us that the downregulation also happens right after a pseudotime value of 16. The temporal coalescence of the loss of Ascl1 expression in the Timecourse experiment with the persistence of cells with pseudotime values > 16 in the Pulse experiment provides strong evidence that we have identified the point at which cells stop expressing Ascl1 while maintaining more mature cell fates. The plots below will be added to the manuscript.

Author response image 2.

(3) It is intriguing to observe that the expression of Ascl1 was down-regulated in both neuronal precursors and bipolar cells in the mouse retina following tamoxifen and NMDA treatment (refer to Fig. 3C). However, the expression of ectopical Ascl1 should have been constitutively activated by tamoxifen. Therefore, if the GFP+ bipolar cells and neuronal precursors were indeed converted from Müller cells, we would expect to capture a high level of Ascl1 expression. How to account for this discrepancy? How is the expression exogenous Ascl1 expressed from a constitutive promoter attenuated?

As discussed above, this has been observed previously. Ascl1 driven from the TTA transgenic mouse line is high in the MG, but declines as these cells are reprogrammed into neurons in vivo or in vitro.  One possibility is that the TTA is not as active in neurons as in MG, but in other lines of transgenic mice, eg. TRE-Atoh1 mice, the transgene continues to be expressed at a high level even in the differentiating neurons, so this downregulation appears to be unique to Ascl1.  We do not understand why Ascl1 levels decline in the differentiating neurons, but this has been a consistent finding across several studies of in vivo and in vitro reprogramming.

(4) Exogenous Ascl1 was shut down after other neuronal specific genes were induced during MG reprogramming in vitro. Is this also the case during Ascl1-mediated reprogramming in vivo? If so, do converting cells show a distinct gene expression program if exogenous Ascl1 is constitutively overexpressed?

Yes, as can be seen in Fig 3C Ascl1 expression is high in the MG and Transition cell populations, but decreases in the NeuPre and Bipolar cells. As stated above, continued high Ascl1 expression keeps cells in a more progenitor-like state. This is true in vivo and in vitro. It has been more clearly addressed upon revision.  

(5) As previously documented in their Science Advances publication, the authors have established the requirement of NMDA injury for facilitating the successful induction of neuronal conversion through Ascl1 over-expression. Why is injury required for MG conversion in vivo, but not in vitro? This is related to question #1 above that certain signals may be required for the full conversion process, not just the initial induction of a few neuronal specific genes.

While the in vitro and in vivo systems share similarities, there are key differences, which affect what must be done to the cells in order to produce converted neurons. In our initial publication demonstrating that Ascl1 can reprogram mouse MG to a neurogenic state, we carried out our experiments in dissociated cell cultures (Pollak et al 2013) like those described in this report.  At that time, we did not need to add either NMDA or TSA to the cultures to induce neurogenesis from Ascl1.  However, when we attempted the reprogramming in vivo, we found that after postnatal day 8, injury and TSA were required in vivo (Ueki et al; Jorstad et al). We surmise that the massive neuronal loss that occurs in establishing dissociated MG cultures replaces the NMDA injury we carry out in vivo.   

To your second point about the requirement for more than “just the initial induction of a few neuronal specific genes”. This is definitely true. When we carry out reprogramming in vivo with Ascl1 or other transcription factors, the MG-derived neurons acquire neuronal morphology, develop neuron-like electrophysiological properties, integrate into the retinal circuit and respond to light stimulus; however, they are still not identical in gene expression or morphology to normal retinal neurons. This  is why we are continuously looking for more compounds or conditions that can help improve the process.

(6) The discovery that Metformin acts as a stimulator for MG-to-neuron conversion is interesting.

However, before drawing definitive conclusions, several questions need to be addressed:

(a) As specific small molecules have been identified to change cell fates, the question is whether Metformin and other effective compounds can function alone or have to effect in conjunction with Ascl1? This can and should be tested in vitro by simply treating MG with Metformin but not doxycycline.

To our knowledge there are no convincing in vivo trials in which neurons have been generated from MG using only combinations of small molecules. Because Metformin was identified in vitro due to the increase in recovered cells and not an increase in % neurons, we especially doubt it would have the desired increase in neurons without expression of a transcription factor.  

(b) Metformin is known to target AMPK, but this is unlikely the only target of the drug. Does AMPK knockdown have the same enhancement effect?

In the drug screen, we also tested the AMPK inhibitor Dorsomorphin dihydrochloride, but it didn’t have any effect. However, Metformin is an activator, so it would be interesting to see in future studies if Dorsomorphin dihydrochloride could inhibit the effect of Metformin or if the enhancement is acting independently.  

(c) Is the effect of Metformin specific for Ascl1 or any TF(s) that stimulates MG-to-neuron conversion?

We would like to follow up with this in future.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary: 

Using concurrent in vivo whole-cell patch clamp and dendritic calcium imaging, the authors characterized how functional synaptic inputs across dendritic arborizations of mouse primary visual cortex layer 2/3 neurons emerge during the second postnatal week. They were able to identify spatially and functionally separated domains of clustered synapses in these neurons even before eye-opening and characterize how the clustering changes from P8 to P13. 

Strengths: 

The work is technically challenging and the findings are novel. The results support previous EM and immunostaining studies but provide in vivo evidence on the time course and the trajectory of how functional synaptic input develops. 

Weaknesses: 

There are some missing details about how the experiments were performed, and I also have some questions about the analyses. 

We have now added a more detailed description of the methods and added new supplemental figures and descriptions to clarify our analyses. Please find our responses to the specific points of this reviewer in the section “Recommendations for the authors” below.

Reviewer #2 (Public Review):

In this study, Leighton et al performed remarkable experiments by combining in-vivo patch-clamp recording with two-photon dendritic Ca2+ imaging. The voltage-clamp mode is a major improvement over the pioneer versions of this combinatorial experiment that has led to major breakthroughs in the neuroscience field for visualizing and understanding synaptic input activities in single cells in-vivo (sharp electrodes: Svoboda et al, Nature 1997, Helmchen et al, Nature Neurosci 1999; whole-cell current-clamp: Jia et al, Nature 2010, Chen et al, Nature 2011. I suggest that these papers would be cited). This is because in voltage-clamp mode, despite the full control of membrane voltage in-vivo not being realistic, is nevertheless most effective in preventing back-propagation action potentials, which would severely confound the measurement of individual synaptically-induced Ca2+ influx events. Furthermore, clamping the cell body at a strongly depolarized potential (here the authors did -30mV) also facilitates the detection of synaptically-induced Ca2+ influx. As a result, the authors successfully recorded high-quality Ca2+ imaging data that can be used for precise analysis. To date, even in view of the rapid progress of voltage-sensitive indicators and relevant imaging technologies in recent years, this very old 'art' of combining single-cell electrophysiology and two-photon imaging (ordinary, raster-scanned, video-rate imaging) of Ca2+ signals still enables measurements of the best level precision. 

We thank the reviewer for reminding us of these important previous studies that we cite now in the revised manuscript. 

On the other hand, the interpretation of data in this study is a bit narrow-minded and lacks a comprehensive picture. Some suggestions to improve the manuscript are as follows: 

(1) The authors made a segregation of 'spine synapse' and 'shaft synapse' based solely on the two photon images in-vivo. However, caution shall be taken here, because the optical resolution under in vivo imaging conditions like this cannot reliably tell apart whether a bright spot within or partially overlapping a segment of the dendrite is a spine on top of (or below) it. Therefore, what the authors consider as a 'shaft synapse' (by detecting Ca2+ hotspots) has an unknown probability of being just a spine on top or below the dendrite. If there is other imaging data of higher axial resolution to validate or calibrate, the authors shall take some further considerations or analysis to check the consistency of their data, as the authors do need such a segregation between spine and shaft synapses to show how they evolve over the brain development stages. 

We agree with the reviewer that the differentiation between spine and sha synapses can be difficult for those spines that are located above or below the dendric sha in the z-dimension because of the lower resolution of 2-photon microscopy in the z-dimension compared to the image plane. We have now added a new paragraph to the Methods section to describe in more detail how we identify spine and sha synapses and provide more examples in a new supplementary figure (Fig S5). We believe that we can identify spine and sha synapses reliably in most cases, but added a cautionary note to make the reader aware of potential misidentifications.

(2) The use of terminology 'bursts of spontaneous inputs' for describing voltage-clamp data seems improper. Conventionally, 'burst' refers to suprathreshold spike firing events, but here, the authors use 'burst' to refer to inward synaptic currents collected at the cell body. Not every excitatory synaptic input (or ensemble of inputs) activation will lead to spike firing under naturalistic conditions, therefore, these two concepts are not equivalent. It is recommended to use 'barrage of inputs' instead of 'burst of inputs'. Imagine a full picture of the entire dendritic tree, the fact that the authors could always capture spontaneous Ca2+ events here and there within a few pieces of dendrites within an arbitrary field-of-view suggests that, the whole dendritic tree must have many more such events going on as a barrage while the author's patch electrode picks up the summed current flow from the whole dendritic tree. 

We agree with the reviewer that “barrage” is a clearer term for multiple synaptic inputs occurring simultaneously and therefore we changed the terminology throughout the manuscript.

(3) Following the above issue, an analysis of the temporal correlation between synaptic (not segregating 'spine' or 'shaft') Ca2+ events and EPSCs is absent. Again, the authors drew arbitrary time windows to clump the events for statistical analysis. However, the demonstrated example data already shows that the onset times of individual synaptic Ca2+ events do not necessarily align with the beginning of a 'barrage' inward current event. 

The reviewer writes that “an analysis of the temporal correlation between synaptic calcium events and EPSCs is absent”. We would like to point out that we did determine the percentage of calcium transients that occurred during barrages of synaptic inputs (~60%, page 7). This is important, since the barrages in our patch-clamp recordings most likely reflect spontaneous network events as described in the developing cortex previously by us and many other labs . The time window we chose was not “arbitrary” as the reviewer suggests, but based on the duration of the barrages of synaptic inputs as defined in the Methods section. 

The reason, why we did not perform a more in-depth analysis of the temporal relationship between synaptic calcium transients and synaptic input currents is that it is essentially impossible to relate calcium transients at individual synapses to specific synaptic input events. First, during barrages of synaptic inputs many synapses are active simultaneously, both in the mapped dendrites as well as in the un-observed parts of the dendric arborization as the reviewer notes above. Thus, barrages cannot be broken down into individual synaptic transmission events. Second, since our acquisition frequency is ~10 Hz, we can identify the onset of individual synaptic calcium transients with 100-200 ms precision (1 or 2 frames). However, throughout any 100-200 ms period of recording, several synapses are active across the entire dendric arborization such that we cannot assign a given calcium transient to a specific EPSC within a 100-200 ms epoch. Third, due to the limited clamping capacity of in vivo patch recordings, we cannot be certain that individual transmission events in distal dendrites can be resolved in the patch recording.

(4) The authors claim that "these observations indicate that the activity patterns investigated here are not or only slightly affected by low-level anesthesia". It would be nice to show some of the recordings in this work without any anesthesia to support this claim. 

Indeed, the conclusion that the patterns of activity are only slightly affected by low levels of anesthesia is based on our previous recordings on the network level. Unfortunately, we are still not able to record calcium imaging with single synapse resolution in unanesthezed developing mice (and no one else is as far as we know), because the skull of these young animals is not firm, yet. As a consequence, movements cannot be reduced sufficiently for patching and imaging with single synapse resolution. Our previously published (Siegel et al., 2012) and unpublished work on the cellular level suggests that activity patterns during light anesthesia are very similar to those during sleep in mouse pups at this age.

Reviewer #3 (Public Review):

Summary: 

There is a growing body of litterature on the clustering of co-active synapses in adult mice, which has important implications for understanding dendritic integration and sensory processing more broadly. However, it has been unclear when this spatial organization of co-active synapses arises during development. In this manuscript, Leighton et al. investigate the emergence of spatially organized, coactive synapses on pyramidal dendrites in the mouse visual cortex before eye-opening. They find that some dendrite segments contain highly active synapses that are co-active with their neighbors as early as postnatal day (P) 8-10, and that these domains of co-active synapses increase their coverage of the dendritic arbor by P12-13. Interestingly, Leighton et al. demonstrate that synapses co-active with their neighbors are more likely to increase their activity across a single recording session, compared to synapses that are not co-active with their neighbors, suggesting local plasticity driven by coincident activity before eye-opening. 

The current manuscript includes some replication of earlier results from the same research group (Winnubst et al., 2015), including the presence of clustered, co-active synapses in the visual cortex of mouse pups, and the finding that synapses co-active with their neighbors show an increase in transmission frequency during a recording session. The main novelty in the current study compared to Winnubst et al. (2015) is the inclusion of younger animals (P8-13 in the current study compared to P10-15 in Winnubst et al., 2015). The current manuscript is the first demonstration that active synapses are clustered on specific dendrite segments as early as P8-10 in the mouse visual cortex, and the first to show the progression in active synapse distribution along the dendrite during the 2nd postnatal week. These results from the visual cortex may help inform our understanding of sensory development more broadly. 

Strengths: 

The authors ask a novel question about the emergence of synaptic spatial organization, and they use well-chosen techniques that directly address their questions despite the challenging nature of these techniques. To capture both structural and functional information from dendrites simultaneously, the authors performed a whole-cell voltage clamp to record synaptic currents arriving at the soma while imaging calcium influx at individual synaptic sites on dendrites. The simultaneous voltage clamp and calcium imaging allowed the authors to isolate individual synaptic inputs without their occlusion by widespread calcium influx from back-propagating action potentials. Achieving in vivo dendrite imaging in live mice that are as young as P8 is challenging, and the resulting data provides a unique view of synaptic activity along individual dendrites in the visual cortex at an early stage in development that is otherwise difficult to assess. 

The authors provide convincing evidence that synapses are more likely to be co-active with their neighbors compared to synapses located farther away (Fig. 6F-H), and that synapses co-active with their neighbors increase their transmission frequency during a recording session (Figure 7C). These findings are particularly interesting given that the recordings occur before eye-opening, suggesting a relationship between co-activity and local synaptic plasticity even before the onset of detailed visual input. These results replicate previously published findings from P10-15 pups (Winnubst et al., 2015), increasing confidence in the reproducibility of the data. 

The authors also provide novel data documenting for the first time spatially organized, co-active synapses in pups as young as P8. Comparing the younger (P8-10) and older (P12-13) pups, provides insight into how clusters of co-active synapses might emerge during development. 

Weaknesses: 

This manuscript provides insufficient detail for assessing the rigor and reproducibility of the methods, particularly for age comparisons. The P8-10 vs P12-13 age comparisons are the primary novel finding in this manuscript, and it is, therefore, critical to avoid systematic age differences in the methods and analysis whenever possible. Specific concerns related to the age comparisons are listed below: 

(1) Given that the same research group previously published P12-13 data (Winnubst et al., 2015), it is unclear whether both age groups in the current study were imaged/analyzed in parallel by the same researcher(s), or whether previous data was used for the P12-13 group. 

While indeed the approach in the present study is similar to that of our previous study (Winnubst et al. 2015), the data set presented here is entirely new. The current study was made possible by a new microscope that allows combining resonant scanning with piezo-focusing to image large fractions of the dendric arborization. In fact, we could now image almost 10 times larger dendric segments including branch points than in our previous study. One author contributed to the experiments in both studies. Image analysis of all experiments was performed by the first author of the present study who was not involved in the Winnubst et al. work.

(2) The authors mention that they used 2 different microscopes, and used a fairly wide range of imaging frame rates (5-15 Hz). It is unclear from the current manuscript whether the same imaging parameters were used across the two age groups. If data for the two experimental groups was collected separately, perhaps at different times, by a different person, or on a different microscope, there is a concern that some differences between the groups may not necessarily be due to age. 

The reviewer mentions that the experimental settings are not identical across the experiments of this study. In the original manuscript we erroneously reported in the Methods section that 2 different setups were used for this study; however, all experiments were performed on the same microscope. We have corrected this in the new manuscript. We took timelapse recordings of small stacks of varying depth to cover as many dendrites as possible in each recording, therefore, we needed to adjust the rate of acquired stacks within a certain range as the reviewer points out. The data were acquired by two scientists during an overlapping period. And while the different ages were not recorded in a strictly randomized fashion, they were not acquired in sequence according to ages, but rather involved many attempts on animals of different ages from many different litters. For each litter a small percentage of animals would generate successful recordings, and the ages of these successes were random. Therefore, we believe that neither the collection of data nor the analysis (see point above) affected the differences we describe here for the two age groups.

(3) It is unclear whether the image analysis was performed blind to age. Blinding to age during analysis is particularly important for this study, in which it was not possible to blind to age during imaging due to visible differences in size and developmental stage between younger and older pups. 

The analysis was not setup to be performed blind to age. Not only is the age of the animal apparent at the stage (as the reviewer points out), also the number of spines and the activity levels clearly show differences between neurons only a few days apart. However, all age-related findings reported in this study - except the increase in synapse density and activity - became apparent to us only after the full set of synaptic transmission events was determined and the analysis was performed on the entire data set, making it very unlikely that event detection was biased.

(4) The relatively low N (where N is the number of dendrites or the number of mice) in this study is acceptable due to the challenging nature of the techniques used, but unintentional sampling bias is a concern. For example, if higher-order dendrites from the apical tuft were imaged at P12-13, while more segments of the apical trunk were imaged at P8-10, this could inadvertently create apparent age differences that were in fact due to dendrite location on the arbor or dendrite depth. 

The reviewer points out that sampling bias with respect to synapse location along dendrites in the dataset could lead to falsely apparent age differences. In all experiments we imaged dendrites of layer 2/3 neurons that were relatively close to the cortical surface to optimize image quality. In addition, we confirmed that the mean distance of the imaged dendric stretches from the cell body was similar between the dendrites of each age group (Young: 392 +/-  104 µm, Old: 323 +/- 118 µm; mean +/- STD). Therefore, we do not think that sampling bias affected these results.

Additional general methodological concerns, which are not specifically related to the age comparisons, are listed below: 

(5) The authors assert that clustered, co-active synapses emerge in the visual cortex before eye-opening, which is an important finding in that it suggests this phenomention is driven by spontaneous activity rather than visual input. However, this finding hinges on the imaged cells being reliably located in the visual cortex, which is difficult to identify with certainty in animals that have not yet opened their eyes and therefore cannot undergo intrinsic signal imaging to demarcate the boundaries of the visual cortex. If the imaged cells were in, for example, nearby somatosensory cortex, then the observed spatial organization could be due to sensory input rather than spontaneous activity. 

The reviewer argues that if the neurons included in our analysis were located in non-visual sensory cortex, e.g. the somatosensory cortex, sensory experience might have shaped clustered inputs instead of spontaneous activity. We are, however, certain that the neurons were located inside the primary visual cortex. In previous experiments where we performed the same craniotomies, we mapped spontaneous activity across the sensory areas in the occipital neocortex and we know the exact location of V1 which is already very consistent during the second postnatal week. (See for example Supplemental Figure 4 in Leighton et al., 2021).  

(6) It is unclear how the authors defined a synaptic transmission event in the GCaMP signal (e.g. whether there was a quantitative deltaF/F threshold). 

In the revised manuscript, we describe the procedure of identifying synaptic calcium transients in more detail and added a new supplemental figure to clarify this aspect of the analysis. In short, we use an automated detection with a 2x standard deviation threshold and a subsequent manual control and selection step. Please, find all details in the Methods section and Figure S4 of the revised manuscript.

(7) The authors' division of synapses into spine vs shaft is unconvincing due to the difficulty of identifying Z-projecting spines in images from 2-photon microscopy, where the Z resolution is insufficient to definitively identify Z-projecting spines, and the fact that spines in young animals may be thin and dim. The authors' examples of spine synapses (e.g. in Fig. 2A) are convincing, but some of the putative shaft synapses may in fact be on spines. 

We agree with the reviewer that the differentiation between spine and sha synapses can be difficult for those spines that are located above or below the dendric sha in the z-dimension because of the lower resolution of 2-photon microscopy in the z-dimension compared to the image plane (see also response to Reviewer 2, point 1). We have now added a new paragraph to the Methods section to describe in more detail how we identify spine and sha synapses and provide more examples in a new supplementary figure (Fig S5). We believe that we can identify spine and sha synapses reliably in most cases, but added a cautionary note to make the reader aware of potential misidentifications.

Reviewer #1 (Recommendations For The Authors):

I think the experiments performed were very technically challenging (probably one of the few labs that can do this in the field), and the findings provide in vivo evidence on how structured synaptic inputs are assembled during development that has never been reported. 

I suggest improving the writing and presentation and really explaining how they conducted the experiments and how they defined shaft synapses. 

Line 96: 12 dendritic areas from 11 mice at ages between postnatal day 8 to 13. 

- Do the authors know how many neurons were imaged? It is unclear if the authors patch on all the imaged neurons and only imaged (or analyzed) the dendrites of those patched neurons. If yes, how sparse are the neurons labelled from IUE? From 1B, it looks like there are two cells adjacent to each other. Can the authors really distinguish whether the imaged dendrites are from the patched neuron? 

The reviewer wonders whether we can tell apart dendrites of patched cells from those of neighboring neurons that were not patched. This is actually very straight forward: the experiment included a depolarization step (see Methods section) which leads to an immediate, but temporary, increase in fluorescence in all of the patched neurons’ dendrites, but none of the neighboring dendrites. We have added this information to the Methods section of the new manuscript and provide now an example (Fig S3). Furthermore, as these cells normally fire frequently, it would immediately become clear that an unpatched cell is being imaged if backpropagating action potentials are predominantly observed rather than synaptic signals. The visualization of these synaptic signals is only possible due to the blockade of Na+ channels with QX314 in the intracellular solution (see Methods). 

- In the methods section, it says 'dendrites were imaged in single plane or small stacks with plane...'. How do the authors do calcium imaging with small stacks of plane using Nikon MP scope? 

Small stacks were acquired by using the piezo focusing device of our Nikon A1 microscope. Since we combined this fast focusing approach with resonant scanning, we were able to acquire z-stacks of 3-5 frames at a rate of up to 15 Hz (per stack).

- I also assume this is not chronic imaging, and there are different mice for each postnatal day. If it's true, this is somewhat important for all the correlation analysis as there are only 2 mice for each postnatal day (other than day 12) and day 13 only has 1 animal. 

Yes, indeed these are not chronic experiments and dendrites imaged on different days are from different neurons and different mice. We agree with the reviewer that if it had been possible to image the same neurons across these developmental stages, we would have detected even clearer correlations. Therefore, we see our results as conservative estimates of the developmental trajectory of the analyzed parameters.

Line 104 - 109: I don't understand why the authors need to hold at -30mV to facilitate calcium influx through NMDA receptors? I assume this helps them to visualize as many synapses as possible? but wouldn't that also make the 'event frequency' not reflect the true value? 

Indeed depolarizing the imaged neurons to -30 mV was necessary to get sufficient calcium influx to map synaptic inputs. We don’t think that this affects the frequency of inputs, because the frequency of synaptic inputs is determined by the presynaptic firing rate and the release probability of the presynaptic terminal, which are not affected by the depolarization of the dendrite.

Figure 2A - It says in the method section that ROIs are manually selected. However, it's not explained what the criteria are. For spine synapses, it's easy to define but for shaft synapses like in Fig 2B, why are there 2 synapses on the shaft? And in Fig 4a, 5a, Fig S1 P13, some of the dendrites are packed with ROIs. What's the distance between those shaft synapses? Can the imaging resolution really separate them? 

The reviewer asks for a better description of how we identified individual ROIs and thus synapse locations and whether this is actually feasible. We have now added a more detailed description of how we select synaptic sites based on the occurrence of synaptic calcium transients. In addition, we have added a new supplemental Figure (S4) to give the reader an impression of the image quality and the ability to locate individual synapses reliably. We find that separating sha synapses was possible for inter-synapse distances of ~4 µm or more. The mean sha synapse distance in our data set is 21 µm.

- Similar issue applies to Figure 4A that I'm not sure what's the resolution of each 'hot spot'. They all seem very close together. Maybe additional raw dendrite images with fluorescence changes like 1C or 2A could be helpful (or movies in the supplementary?) 

As the reviewer suggests, we have added now additional supplemental figures to illustrate better how we identify synaptic transmission events as well as spine and sha synapses.

- Also for line 164, it says that 76% of high-activity synapses were located on spines. This could also maybe support that only the spine synapses are real synapses and many shaft synapses are actually not synapses and they were just categorized as shaft synapses from manual ROI? 

We are actually quite sure that sha synapses are real synapses based on our analysis, since they show repeated synaptic calcium transients that co-occur with barrages of synaptic inputs as measured by patch-clamp recordings. Indeed one would expect to see a number of excitatory synapses on dendric shas of pyramidal neurons at these ages based on previous EM studies (Miller and Peters, 1981; Wildenberg et al., 2023).

- While this might not impact the overall novelty of the paper, I would be curious to know if the authors can still observe the same findings if they only analyze spine synapses. 

We repeated several analyses with a dataset that contained only spine synapses. For most analyses we observed the expected result: the effect sizes were similar compared to the entire data set, but the power was reduced. For example the effect of distance to closest high-activity neighbor and own activity (Fig 5E, F) was similar, but p-values were around 0.1 (Similar results for Figure 7B). In contrast, the co-activity with synapses within a domain was significantly higher than the co-activity with synapses in other domains also for the spine-synapse only data set. 

Fig 6 - Does the domain co-activity also contribute to the synaptic current recorded (related to Fig 4). 

Yes, the synaptic activity measured by calcium imaging contributes to the recorded EPSCs. However, the exact relationship between synaptic inputs measured by calcium imaging and those measured by patch-clamping is complicated by 3 factors: first, during barrages of synaptic inputs many synapses are active simultaneously, both in the mapped dendrites as well as in the un-observed parts of the dendric arborization. Thus, barrages cannot be broken down into individual events. Second, since our acquisition frequency is ~10 Hz, we can identify the onset of individual synaptic calcium transients with 100-200 ms precision (1 or 2 frames). However, throughout any 100-200 ms period of recording several synapses are active across the entire dendric arborization such that we cannot assign a given calcium transient to a specific EPSC within a 100-200 ms epoch. Third, due to the limited clamping capacity of in vivo patch recordings, we cannot be certain that individual transmission events in distal dendrites can be resolved in the patch recording as EPSCs.

Reviewer #2 (Recommendations For The Authors):

(1) I suggest the authors should provide the number of cells and mice recorded in the figure legends. 

The number of dendrites and mice is the same across all analyses: 12 dendrites from 11 mice for all experiments, 6/6 for P8-10 and 6/5 for P12-13. All dendrites and synapses (and their ages) are shown in the supplemental figures S1 and S2. We mention the number of imaged dendrites now at the beginning of the Results section and when we split ages for the first me.

(2) Instead of showing only cartoon illustrations of dendrites in Figures 3-6, I suggest showing the two photon images as well together with the cartoon. 

The 2-photon images of all dendrites of the dataset are available in Figure S1. To allow the reader to compare the cartoon representations in the main figures and the 2-photon images of each neuron, we have now labeled each dendrite in the dataset (D1-D12, see figures S1 and S2). For every figure, where we show example neurons (cartoons or zoom ins) we now provide this identifier.

Reviewer #3 (Recommendations For The Authors):

To address the weaknesses outlined above, we recommend that the authors do the following: 

• To address concerns about the rigor and reproducibility of the methods specifically related to age comparisons, please confirm the following: 

- Both age groups were run in parallel by the same researcher(s). 

Experiments were run partly overlapping and experiments from different age groups were performed in parallel by both researchers.

- Both age groups were imaged on the same microscope, or animals from each age group were imaged on both microscopes. If it was necessary to use different microscopes for the different age groups for biological or practical reasons, please explain. 

All experiments were run on the same microscope, a Nikon A1 2-photon microscope. In the original methods description we erroneously mentioned two microscopes (copy and paste error from a previous publication). We corrected that in the revised manuscript.

- There was no difference in imaging frame rates or other imaging parameters between age groups. If it was necessary to use different parameters for different age groups for biological reasons, please explain. 

We varied the frame rates somewhat to allow larger z-stacks for some experiments where dendrites traversed different depths; however the mean frame rates were similar between the experiments in P8-10 vs P12-13 dendrites, 8.5 vs 10 Hz, respectively.

- Images were analyzed blind to age. 

The analysis was not setup to be performed blind to age. The number of spines and the activity levels clearly show obvious differences between neurons only a few days apart. However, all findings reported in this study related to age - except the increase in synapse density and activity - became apparent to us only after the full set of synaptic transmission events was determined and the analysis was performed on the entire data set, making it unlikely that event detection was biased.

- There was no difference in the location of analyzed dendrites (e.g. depth from the pia, branch order) between age groups. 

In all experiments we imaged dendrites of layer 2/3 neurons that were relatively close to the cortical surface to optimize image quality. In addition, we determined the mean distance of the imaged dendric stretches from the cell body and found that this distance was similar between the dendrites of each age group (Young: 392 +/-  104 µm, Old: 323 +/- 118 µm; mean +/- STD). Therefore, we do not think that sampling bias affected these results.

• To address general methodological concerns, please provide additional description of the following points: 

- Please clarify how the visual cortex was identified in P8-13 pups. If there was ambiguity about identifying the visual cortex in these pups, please discuss the implications of this ambiguity. 

The reviewer asks how we identified V1 in these experiments. We are indeed certain that the neurons were located inside the primary visual cortex. We have ample experience with mapping V1 in these animals based on patterns of spontaneous activity as well as post-hoc stainings. V1 is quite large already at these ages (> 2 mm long and > 1 mm wide) and its extent very consistent across animals. Thus, we would argue it is actually hard to miss.

- Please clarify how synaptic transmission events were identified in the GCaMP signal. 

We have now added a more detailed description of how we identify synaptic calcium transients. In addition, we have added a new supplemental Figure (S3) to give the reader an impression of the image quality and the ability to locate individual synapses reliably. 

- It is acceptable to use the spine vs shaft analysis despite the inevitable difficulty resolving Z-projecting spines, but this caveat should be mentioned in the discussion of the spine vs shaft results. 

We added a more detailed description of spine and sha synapse identification, a new supplemental figure (S5) and we now mention the caveat related to the limited z-resolution of 2-photon microscopy in the revised manuscript.

• Two additional minor details should be clarified in the text of the manuscript: 

- Please specify the volume of DNA solution injected into each embryo. 

The injected volume was 1 µl. We added this information in the Methods section of the revised manuscript.

- In Fig S1, please specify whether the scale bar applies to all images. 

The scale bar applies to all images. This information was added to the figure legend.

References

Leighton AH, Cheyne JE, Houwen GJ, Maldonado PP, De Winter F, Levelt CN, Lohmann C. 2021. Somatostatin interneurons restrict cell recruitment to renally driven spontaneous activity in the developing cortex. Cell Rep 36:109316. doi:10.1016/j.celrep.2021.109316

Miller M, Peters A. 1981. Maturation of rat visual cortex. II. A combined Golgi-electron microscope study of pyramidal neurons. JComp Neurol 203:555–573.

Siegel F, Heimel JA, Peters J, Lohmann C. 2012. Peripheral and central inputs shape network dynamics in the developing visual cortex in vivo. Current Biology 22:253–258.

Wildenberg G, Li H, Sampathkumar V, Sorokina A, Kasthuri N. 2023. Isochronic development of cortical synapses in primates and mice. Nat Commun 14:8018. doi:10.1038/s41467-02343088-3

Author response:

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

Reviewer #1 (Public Review):

This is an interesting and well-written paper reporting on a novel approach to studying cerebellar function based on the idea of selective recruitment using fMRI. The study is well-designed and executed. Analyses are sound and results are properly discussed. The paper makes a significant contribution to broadening our understanding of the role of the cerebellum in human behavior.

We thank the reviewer for the positive assessment of our paper.

(1) While the authors provide a compelling case for the link between BOLD and the cerebellar cortical input layer, there remains considerable unexplained variance. Perhaps the authors could elaborate a bit more on the assumption that BOLD signals mainly reflect the input side of the cerebellum (see for example King et al., elife. 2023 Apr 21;12:e81511).

Our paper is based on the assumption that the cerebellar BOLD signal reflects solely the input to the cerebellum and does not reflect the changes in firing rates of Purkinje cells. This assumption relies on two lines of arguments: Studies that have directly looked at the mechanism of vasodilation in the cerebellum, and studies that try to infer the contributions of different neurophysiological mechanisms to overall cerebellar metabolism (Attwell and Iadecola, 2002).

Vasodilatory considerations: The mechanisms that causes vasodilation in the cerebellum, and hence BOLD signal increases, has been extensively studied: Electrical stimulation of mossy fibers (Gagliano et al., 2022; Mapelli et al., 2017), as well as parallel fibers (Akgören et al., 1994; Iadecola et al., 1996; Mathiesen et al., 1998; Yang and Iadecola, 1997) lead to robust increases in cerebellar blood flow. In contrast to the neocortex, the regulation of blood flow in the cerebellum depends nearly purely on the vasodilator Nitric Oxide (NO) (Akgören et al., 1994; Yang and Iadecola, 1997) with stellate cells playing a key role in the signaling cascade (Yang et al., 2000).

Electrical (Mathiesen et al., 2000) and pharmacological (Yang and Iadecola, 1998) stimulation of climbing fibers also leads to robust increases in blood flow. Simultaneous parallel and climbing fiber stimulation seems to combine sub-additively to determine the blood flow changes (K. Caesar et al., 2003).

Importantly, even dramatic changes in spiking rate of Purkinje cells do not lead to changes in vasodilation. For starters, parallel fiber stimulation leads to blood flow increases, even though the net effect on Purkinje cell firing is inhibitory (Mathiesen et al., 1998). More importantly, complete inhibition of the Purkinje cell using a GABA agonist does not change baseline cerebellar blood flow (Kirsten Caesar et al., 2003). Conversely, even a 200-300% increase in simple (and complex) spike firing rate through application of a GABA antagonist does not show any measurable consequences for blood flow, even though it clearly increases the metabolic rate of oxygen consumption in the tissue (Thomsen et al., 2009, 2004).

In sum, this extensive set of studies clearly argues that the cerebellar blood flow response is mostly dictated by synaptic input, and that the firing rate of Purkinje cells does not influence vasodilation. Because the BOLD signal is caused by an supply of oxygen over and above the level of oxygen consumption, this would argue that increases in Purkinje cell firing would not lead to BOLD increases. What is less clear is the degree to which changes in BOLD signal during normal activity are determined by changes in mossy fiber or climbing fiber input. Disruption of either pathway leads to 60-70% reductions in the evoked blood flow response during whisker stimulation (Yang et al., 2000; Zhang et al., 2003) – but it remains unclear to what degree this reflects the distribution of contributions in the healthy animal, as these powerful disruptions may have a number of side-effects.

Metabolic considerations: To estimate the relative contributions climbing fiber / mossy fiber input to the variations in BOLD signal under natural conditions, it is useful to consider the contributions of different cerebellar processes to the overall metabolism of the cerebellum. Assuming an average firing rate of 40Hz for mossy fibers, ~3Hz for Granule cells, and 1Hz for climbing fibers, Howarth et al. (Howarth et al., 2012, 2010) estimated that the transmission from mossy fibers to granular cells, dominates the energy budget with 53%. The subsequent stage, encompassing the transfer of information from Granular cells to Purkinje cells, accounts for 32% of energy expenditure. In contrast, integration within Purkinje cells and the spiking (simple and complex) of these cells represents only 15% of the total energy consumption.

More important for the BOLD signal, however, are the activity-induced variations in metabolic consumption: Purkinje cells fire relatively constantly at a very high frequency (~50Hz) both during awake periods and during sleep (Shin et al., 2007). When providing a signal to the neocortex, firing rate decreases, actually lowering the metabolic demand. Climbing fibers normally fire at ~0.5 Hz and even during activity rarely fire much above 2Hz (Streng et al., 2017). In contrast, granule cells show a low firing rates during rest (typically <1hz) and can spike during activity well above 100Hz. Combined with the sheer number of granule cells, these considerations would suggest that the vast majority of the variation in metabolic demand are due to mossy fiber input and granule cell activity.

Overall, we therefore think it is likely that the main determinant of the cerebellar cortical BOLD signal is mossy fiber input and the transmission of information from mossy fibers to granule cells to Purkinje cells. We admit that the degree to which climbing fiber input contribute to BOLD signal changes is much less clear. We can be quite certain, however, that the firing rate of Purkinje cells does not contribute to the cerebellar BOLD signal, as even dramatic changes in the firing rate do not cause any changes in vasodilation.  We have clarified our line of reasoning in the paper, and hope this more extensive response here will give the reader a better overview over the pertaining literature.

(2) The current approach does not appear to take the non-linear relationships between BOLD and neural activity into account.

Thank you for raising this concern. We did not stress this point in the paper, but one big advantage of our selective recruitment approach is that it is – to some degree- robust against non-linearities in the relationship between neural activity and BOLD signal. This is the case, as long as the shape of the non-linearity is similar in the cerebellum and the neocortex. The results of our motor task (Figure 3) provide a clear example of this: The BOLD signal both in the neocortex and cerebellum incases non-linearly as a function of force – the increase from 2.5N to 6N (a 3.5N increase) is larger than the increase from 6N to 10N (a 4N increase). A similar non-linearity can be observed for tapping speed (6, 10 to 18 taps / s). However, within each condition, the relationship between cortical and cerebellar activity is nearly perfectly linear, reflecting the fact that the shape of the non-linearity for the cerebellum and cortex is very similar.

Most importantly, even if the non-linearity across the two structures is different, any non-linear relationship between neural activity and BOLD signal (of vasodilatory nature) should apply to different conditions (here force and speed increases) similarly. Therefore, if two conditions show overlapping activity levels (as observed for force and speed across medium and high levels, Figure 3), a offset between conditions cannot be caused by a non-linearity in the relationship of cortical and cerebellar activity. Because all conditions are subject to the same non-linearity, all points should lie on a single (likely monotonically increasing) non-linear function. Both for the motor and working memory task, the pattern of results clearly violates this assumption.

(3) The authors may want to address a bit more the issue of closed loops as well as the underlying neuroanatomy including the deep cerebellar nuclei and pontine nuclei in the context of their current cerebello-cortical correlational approach. But also the contribution of other brain areas such as the basal ganglia and hippocampus. 

Cortical-cerebellar communication is of course bi-directional. As discussed in King at al., (2023), however, we are restricting our model to the connections from the neocortex to the cerebellum for the following reasons: First, cerebellar BOLD activity likely reflects mostly neocortical input (see our answer to pt. 1), whereas neocortical activity is determined by a much wider array of projections, including striato-thalamo-cortical and cortico-cortical connections. Secondly, the output of the cerebellum cannot be predicted from the BOLD signal of the cerebellar cortex, as it is unlikely that the firing rate of Purkinje cells contribute to cerebellar BOLD signal (see pt. 1). For these reasons we believe that the relationship between neocortical and cerebellar activity patterns is mostly dictated by the connectivity from cortex to cerebellum, and is therefore best modelled as thus. This is now more clearly discussed in a new paragraph (line 318-323) of the revised manuscript.

We are also ignoring other inputs to the cerebellum, including the spinal chord, the basal ganglia (Bhuvanasundaram et al., 2022; Bostan and Strick, 2018) hippocampus (Froula et al., 2023; Watson et al., 2019), and amygdala (Farley et al., 2016; Jung et al., 2022; Terburg et al., 2024). In humans, however, the neocortex remains the primary source of input to pontine nuclei. Consequently, it stands as the main structure shaping activity within the cerebellar cortex. While it is an interesting question to what degree the consideration of subcortical structures can improve the prediction of cerebellar activity patterns, we believe that considering the neocortex provides a good first approximation.

Reviewer #1 (Recommendations):

(4)  A few sentences to clarify the used models as was done in the King et al. (2024) paper may improve readability.

We have now added the sentences in the introduction (line 25ff):

To approach this problem, we have recently developed and tested a range of cortical-cerebellar connectivity models (King et al., 2023), designed to capture fixed, or task-invariant, transmission between neocortex and cerebellum. For each cerebellar voxel, we estimated a regularized multiple regression model to predict its activity level across a range of task conditions (King et al., 2019) from the activity pattern observed in the neocortex for the same conditions. The models were then evaluated in their ability to predict cerebellar activity in novel tasks, again based only on the corresponding neocortical activity pattern. Two key results emerged from this work. First, while rs-FC studies (Buckner et al., 2011; Ji et al., 2019; Marek et al., 2018) have assumed a 1:1 mapping between neocortical and cerebellar networks, models which allowed for convergent input from multiple neocortical regions to a single cerebellar region performed better in predicting cerebellar activity patterns for novel tasks. Second, when given a cortical activation pattern, the best performing model could predict about 50% of the reliable variance in the cerebellar cortex across tasks (King et al., 2023).

(5) To what extent does this paper demonstrate the limitations of BOLD in neuroscientific research? 

The primary objective of this study was to shed light on the problems of interpreting BOLD activation within the cerebellum. The problem that the BOLD signal mostly reflect input to a region is not unique to the cerebellum, but also applies (albeit likely to a lesser degree) to other brain structures. However, the solution we propose here critically hinges on three features of the cerebellar circuitry: a) the mossy fiber input for the cerebellar hemispheres mostly arise from the neocortex, b) the BOLD signal is likely dominated by this mossy fiber input (see pt. 1), and c) there is very little excitatory recurrent activity in the cerebellum, so output activity in the cerebellum does not cause direct activity in other parts of the cerebellum.

These features motivate us to use a directed cortex->cerebellum connectivity model, which does not allow for any direct connectivity within the cerebellum. While the same approach can also be applied to other brain structures, it is less clear that the approach would yield valid results here. For example, due the local excitatory recurrent connectivity within neocortical columns, the activity here will also relate to local processing.

(6) What if the authors reversed their line of reasoning as in that cerebellum activity is matched to map changes in cerebral cortical activity? Perhaps this could provide further evidence for the assumed directional specificity of the task-dependent gating of neocortical inputs. 

Given (a) that the cerebellar BOLD signal tells us very little about cerebellar output signals (b) that there are many other input signals to the neocortex that are more powerful than cerebellar inputs, and c) that there strong cortical-cortical connections, we believe that this model would be hard to interpret (see also our answer to pt. 3).

Therefore, while the inversion of the linear task-invariant mapping between cortical and cerebellar activity is a potentially interesting exercise, it is unclear to us at this point what strong predictions we would be able to test with this approach.

(7) The statement that cerebellar fMRI activity may simply reflect the transmission of neocortical activity through fixed connections can be better explained. Also in the context of using the epiphenomenon (on page 11) in the paper. To what extent is the issue of epiphenomenon not a general problem of fMRI research?

We have rephrased the introduction of this idea (line 17):

This means that increases in the cerebellar BOLD signal could simply reflect the automatic transmission of neocortical activity through fixed anatomical connections. As such, whenever a task activates a neocortical region, the corresponding cerebellar region would also be activated, regardless of whether the cerebellum is directly involved in the task or not.

Epiphemonal activity: This is indeed a general problem in fMRI research (and indeed research that uses neurophysiological recordings, rather than manipulations of activity). Indeed, we have discussed similar issues in the context of motor activity in ipsilateral motor cortex (Diedrichsen et al., 2009). However, given that we only offer a possible approach to address this issue for the cerebellum (see pt. 5), we thought it best to keep the scope of the discussion focused on this structure.

Reviewer #2 (Public Review):

Summary:

Shahshahani and colleagues used a combination of statistical modelling and whole-brain fMRI data in an attempt to separate the contributions of cortical and cerebellar regions in different cognitive contexts.

Strengths:

The manuscript uses a sophisticated integration of statistical methods, cognitive neuroscience, and systems neurobiology.

The authors use multiple statistical approaches to ensure robustness in their conclusions.

The consideration of the cerebellum as not a purely 'motor' structure is excellent and important. <br />

We thank the reviewer for their positive evaluation.

Weaknesses:

(1) Two of the foundation assumptions of the model - that cerebellar BOLD signals reflect granule cells > purkinje neurons and that corticocerebellar connections are relatively invariant - are still open topics of investigation. It might be helpful for the reader if these ideas could be presented in a more nuanced light.

Please see response to the comment 1 of Reviewer 1 for a more extensive and detailed justification of this assumption. We have now also clarified our rationale for this assumption better in the paper on line 10-14. Finally, we now also raise explicitly the possibility that some of the violations of the task-invariant model could be caused by selectively increase of climbing fiber activity in some tasks (line 340).

(2) The assumption that cortical BOLD responses in cognitive tasks should be matched irrespective of cerebellar involvement does not cohere with the idea of 'forcing functions' introduced by Houk and Wise. 

We are assuming that you refer to the idea that cerebellar output is an important determinant of the dynamics (and likely also of the magnitude) of neocortical activity. We agree most certainly here. However, we also believe that in the context of our paper, it is justified to restrict the model to the connectivity between the neocortex and the cerebellum only (see reviewer 1, comment 3).

Furthermore, if increased cerebellar output indeed occurs during the conditions for which we identified unusually high cerebellar activity, it should increase neocortical activity, and bring the relationship of the cerebellar and cortical activity again closer to the predictions of the linear model. Therefore, the identification of functions for which cerebellar regions show selective recruitment is rather conservative.

Reviewer #2 (Recommendations):

(3) One of the assumptions stated in the abstract -- that the inputs to the cerebellum may simply be a somewhat passive relay of the outputs of the cerebral cortex -- has been challenged recently by work from Litwin-Kumar (Muscinelli et al., 2023 Nature Neuroscience), which argues for complex computational relationships between cortical pyramidal neurons, pontine nuclei and granule cells, which in turn would have a non-linear impact on the relationship between cortical and cerebellar BOLD. The modelling is based on empirical recordings from Wagner (2019, Cell) which show that the synaptic connections between the cortex and granule cells change as a function of learning, further raising concerns about the assumption that the signals inherent within these two systems should be identical. Whether these micro-scale features are indicative of the macroscopic patterns observed in BOLD is an interesting question for future research, but I worry that the assumption of direct similarity is perhaps not reflective of the current literature. The authors do speak to these cells in their discussion, but I believe that they could also help to refine the authors' hypotheses in the manuscript writ large.

We absolutely agree with your point. However, we want to make extremely clear here that our hypothesis (that the inputs to the cerebellum are a linear task-invariant function of the outputs of the cerebral cortex) is the Null-hypothesis that we are testing in our paper. In fact, our results show the first empirical evidence that task-dependent gating may indeed occur. In this sense, our paper is consistent with the theoretical suggestion of (Muscinelli et al., 2023).

You may ask whether a linear task-invariant model of cortical-cerebellar connectivity is not a strawman, given that is most likely incorrect. However, as we stress in the discussion (line 298-), a good Null-model is a useful model, even if it is (as all models) ultimately incorrect. Without it, we would not be able to determine which cerebellar activity outstrips the linear prediction. The fact that this Null-model itself can predict nearly 50% of the variance in cerebellar activity patterns across tasks at a group level, means that it is actually a very powerful model, and hence is a much more stringent criterion for evidence for functional involvement than just the presence of activity.

(4) Further to this point, I didn't follow the authors' logic that the majority of the BOLD response in the cerebellum is reflective of granule cells rather than Purkinje cells. I read through each of the papers that were cited in defense of the comment: "The cerebellar BOLD signal is dominated by mossy fiber input with very little contribution from the output of the cerebellar cortex, the activity of Purkinje cells" and found that none of these studies made this same direct conclusion. As such, I suggest that the authors soften this statement, or provide a different set of references that directly confirm this hypothesis. 

Please see response to the comment 1, Reviewer 1. We hope the answer provides a more comprehensive overview over the literature, which DOES show that spiking behavior of Purkinje cells does not influence vasodilation (as opposed to mossy fiber input). We have now clarified our rationale and the exact cited literature on line 9-14 of the paper.

(5) Regarding the statement: "As such, whenever a task activates a neocortical region, we might observe activity in the corresponding cerebellar regions regardless of whether the cerebellum is directly involved in the task or not." -- what if this is a feature, rather than a bug? That is, the organisation of the nervous system has been shaped over phylogeny such that every action, via efference copies of motor outputs, is filtered through the complex architecture of the cerebellum in order to provide a feed-forward signal to the thalamus/cortex (and other connected structures). Houk and Wise made compelling arguments in their 1995 Cerebral Cortex paper arguing that these outputs (among other systems) could act as 'forcing functions' on the kinds of dynamics that arise in the cerebral cortex. I am inclined to agree with their hypothesis, where the implication is that there are no tasks that don't (in some way) depend on cerebellar activity, albeit to a lesser or greater extent, depending on the contexts/requirements of the task. I realise that this is a somewhat philosophical point, but I do think it is important to be clear about the assumptions that form the basis of the reasoning in the paper. 

This is an interesting point. Our way of thinking about cerebellar function does indeed correspond quite well to the idea of forcing functions- the idea that cerebellar output can “steer” cortical dynamics in a particular way. However, based on patient and lesion data, it is also clear that some cortical functions rely much more critically on cerebellar input than others. We hypothesize here that cerebellar activity is higher (as compared to the neocortical activity) when the functions require cerebellar computation.

We also agree with the notion that cerebellar contribution is likely not an all-or-none issue, but rather a matter of gradation (line 324ff).

(6) Regarding the logic of expecting the cortical patterns for speed vs. force to be matched -- surely if the cerebellum was involved more in speed than force production, the feedback from the cerebellum to the cortex (via thalamus) could also contribute to the observed differences? How could the authors control for this possibility? 

Our model currently indeed does not attempt to quantify the contributions of cerebellar output to cortical activity. However, given that cerebellar output is not visible in the BOLD signal of the cerebellum (see reviewer 1, comment 1), we believe that this is a rational approach. As argued in our response to your comment 2, increased cerebellar output in the speed compared to the force condition should bring the activity relationship closer to the linear model prediction. The fact that we find increased cerebellar (as compared to neocortical) activity in the speed conditions, suggests that there is indeed task-dependent gating of cortical projections to the cerebellum.

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Author response:

eLife assessment:

The manuscript establishes a sophisticated mouse model for acute retinal artery occlusion (RAO) by combining unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) with a silicone wire embolus and carotid artery ligation, generating ischemia-reperfusion injury upon removal of the embolus. This clinically relevant model is useful for studying the cellular and molecular mechanisms of RAO. The data overall are solid, presenting a novel tool for screening pathogenic genes and promoting further therapeutic research in RAO.

Thank you for recognizing the sophistication and clinical relevance of our mouse model for acute retinal artery occlusion. We are grateful for your supportive feedback.

Public Reviews:

Reviewer #1:

Summary:

Wang, Y. et al. used a silicone wire embolus to definitively and acutely clot the pterygopalatine ophthalmic artery in addition to carotid artery ligation to completely block the blood supply to the mouse inner retina, which mimics clinical acute retinal artery occlusion. A detailed characterization of this mouse model determined the time course of inner retina degeneration and associated functional deficits, which closely mimic human patients. Whole retina transcriptome profiling and comparison revealed distinct features associated with ischemia, reperfusion, and different model mechanisms. Interestingly and importantly, this team found a sequential event including reperfusion-induced leukocyte infiltration from blood vessels, residual microglial activation, and neuroinflammation that may lead to neuronal cell death.

Strengths:

Clear demonstration of the surgery procedure with informative illustrations, images, and superb surgical videos.

Two-time points of ischemia and reperfusion were studied with convincing histological and in vivo data to demonstrate the time course of various changes in retinal neuronal cell survivals, ERG functions, and inner/outer retina thickness.

The transcriptome comparison among different retinal artery occlusion models provides informative evidence to differentiate these models.

The potential applications of the in vivo retinal ischemia-reperfusion model and relevant readouts demonstrated by this study will certainly inspire further investigation of the dynamic morphological and functional changes of retinal neurons and glial cell responses during disease progression and before and after treatments.

We sincerely appreciate your detailed and positive feedback. These evaluations are invaluable in highlighting the significance and impact of our work. Thank you for your thoughtful and supportive review.

Weaknesses:

It would be beneficial to the manuscript and the readers if the authors could improve the English of this manuscript by correcting obvious grammar errors, eliminating many of the acronyms that are not commonly used by the field, and providing a reason why this complicated but clever surgery procedure was designed and a summary table with the time course of all the morphological, functional, cellular, and transcriptome changes associated with this model.

Thank you for your thorough review of the manuscript. We sincerely apologize for any grammatical errors resulting from our English language proficiency and have taken the necessary steps to polish the article. Additionally, we have heeded your advice and reduced the use of field-specific acronyms to enhance readability for both the manuscript and its readers.

Regarding the rationale behind the design of the UPOAO model, we have provided a description in Introduction section. Our group focuses on the research of pathogenesis and clinical treatment for RAO. The absence of an accurate mouse model simulating the retinal ischemic process has hampered progress in developing neuroprotective agents for RAO. To better simulate the retinal ischemic process and possible ischemia-reperfusion injury following RAO, we developed a novel vascular-associated mouse model called the unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) model. We drew inspiration from the widely employed middle cerebral artery occlusion (MCAO) model, commonly used in cerebral ischemic injury research, which guided the development of the UPOAO model.

We appreciate your valuable suggestion regarding the inclusion of a summary table outlining the time course of morphological, functional, cellular, and transcriptome changes associated with this model. To address this, we intend to include a supplementary table at the end of the article, which will offer a comprehensive overview of the experimental results, thereby aiding in clarity and interpretation.

Once again, we thank you for your insightful comments and suggestions, which have greatly contributed to the improvement of our manuscript.

Reviewer #2:

Summary:

The authors of this manuscript aim to develop a novel animal model to accurately simulate the retinal ischemic process in retinal artery occlusion (RAO). A unilateral pterygopalatine ophthalmic artery occlusion (UPOAO) mouse model was established using silicone wire embolization combined with carotid artery ligation. This manuscript provided data to show the changes in major classes of retinal neural cells and visual dysfunction following various durations of ischemia (30 minutes and 60 minutes) and reperfusion (3 days and 7 days) after UPOAO. Additionally, transcriptomics was utilized to investigate the transcriptional changes and elucidate changes in the pathophysiological process in the UPOAO model post-ischemia and reperfusion. Furthermore, the authors compared transcriptomic differences between the UPOAO model and other retinal ischemic-reperfusion models, including HIOP and UCCAO, and revealed unique pathological processes.

Strengths:

The UPOAO model represents a novel approach to studying retinal artery occlusion. The study is very comprehensive.

We greatly appreciate your positive assessment of our work and are encouraged by your recognition of its significance.

Weaknesses:

Some statements are incorrect and confusing. It would be helpful to review and clarify these to ensure accuracy and improve readability.

We sincerely appreciate your meticulous review of the manuscript. Taking into account your valuable feedback, we will thoroughly address the inaccuracies identified in the revised version. Additionally, we will commit to polishing the article to ensure improved readability. We apologize for any confusion caused by these inaccuracies and genuinely thank you for bringing them to our attention.

Author response:

We deeply appreciate the editors’ and reviewers’ invaluable time and effort. We would also like to extend our gratitude to eLife for its unwavering commitment to a transparent review and publication model. Below, we present our point-by-point responses to the comments.  

Besides the WT allele, equivalent to the mouse TMEM173 gene, the human TMEM173 gene has two common alleles: the HAQ and AQ alleles carried by billions of people. The main conclusions and interpretation, summarized in the Title and Abstract, are (i) Different from the WT TMEM173 allele, the HAQ or AQ alleles are resistant to STING activation-induced cell death; (ii) STING residue 293 is critical for cell death; (iii) HAQ, AQ alleles are dominant to the SAVI allele; iv) One copy of the AQ allele rescues the SAVI disease in mice. We propose that STING research and STING-targeting immunotherapy should consider human TMEM173 heterogeneity. These interpretations and conclusions were based on Data and Logic. We welcome alternative, logical interpretations from our peers and potential collaborations to advance the human TMEM173 research.  

Reviewer #1 (Public Review):

Responses to Comment 1: We greatly appreciate Reviewer 1's insights. We will change the “lymphocytes” to “splenocytes” (line 134) as suggested. We respectfully disagree with Reviewer 1’s comments on TBK1 (lines 129 – 134). First, we used two different TBK1 inhibitors: BX795 and GSK8612. Second, because BX795 also inhibits PDK1, we used a PDK1 inhibitor GSK2334470; Third, both BX795 and GSK8612 completely inhibited diABZI-induced splenocyte cell death (Figure 1B). The logical conclusion is “TBK1 activation is required for STING-mediated mouse spleen cell death ex vivo”. (line 118). 

This manuscript uncovers a significant aspect of the interplay between the common human TMEM173 alleles and the rare SAVI mutation (lines 23-26). Our discovery that the common human TMEM173 alleles are resistant to STING activation-induced cell death is a substantial finding. It further strengthens the argument that the HAQ and AQ alleles are functionally distinct from the WT allele 1-3. We wish to underscore the crucial message of this study-that 'STING research and STING-targeting immunotherapy should consider TMEM173 heterogeneity in humans' (line 37), which has been largely overlooked in current STING clinical trials 4.  

Regarding STING-Cell death, as we stated in the Introduction (lines 62-79). (i) STING-mediated cell death is cell type-dependent 5-7 and type I IFNs-independent 5,7,8. (ii) The in vivo biological significance of STING-mediated cell death is not clear 7,8. (iii) The mechanisms of STING-Cell death remain controversial. Multiple cell death pathways, i.e., apoptosis, necroptosis, pyroptosis, ferroptosis, and PANoptosis, are proposed 7,9,10. SAVI patients (WT/SAVI) and mouse models had CD4 T cellpenia 8,11. SAVI/HAQ, SAVI/AQ restored T cells in mice. Thus, the manuscript provides some answers to the biological significance of STING-cell death. Next, splenocytes from Q293/Q293 mice are resistant to STING cell death. The logical conclusion is that the amino acid 293 is critical for STING cell death. How aa293 mediates this function needs future investigation. Similarly, how TBK1 mediates STING cell death, independent of type I IFNs and NFκB induction, needs future investigation.

Responses to Comment 2: These are all very interesting questions that we will address in future studies. This manuscript, titled “The common TMEM173 HAQ, AQ alleles rescue CD4 T cellpenia, restore T-regs, and prevent SAVI (N153S) inflammatory disease in mice” does not focus on Q293 mice. We have been researching the common human TMEM173 alleles since 2011 from the discovery12 , mouse model1,3, human clinical trial2, and human genetics studies 3. This manuscript is another step towards understanding these common human TMEM173 alleles with the new discovery that HAQ, AQ are resistant to STING cell death. 

Responses to Comment 3: We aim to address these worthy questions in future studies. In this manuscript, Figure 6 shows AQ/SAVI had more T-regs than HAQ/SAVI (lines 246 – 256). In our previous publication on HAQ, AQ knockin mice, we showed that AQ T-regs have more IL-10 and mitochondria activity than HAQ T-regs 3. We propose that increased IL-10+

Tregs in AQ mice may contribute to an improved phenotype in AQ/SAVI compared to

HAQ/SAVI. However, we are not excluding other contributions (e.g. metabolic difference) by the AQ allele. We will explore these possibilities in future research.   

Responses to Comment 4: Figure 2 is necessary because it reveals the difference between mouse and human STING cell death. Figure 2A-2B showed that STING activation killed human CD4 T cells, but not human CD8 T cells or B cells. This observation is different from Figure 1A, where STING activation killed mouse CD4, CD8 T cells, and CD19 B cells, revealing the species-specific STING cell death responses. Regarding human CD8 T cells, as we stated in the Discussion (lines 318-320), human CD8 T cells (PBMC) are not as susceptible as the CD4 T cells to STING-induced cell death 8. We used lung lymphocytes that showed similar observations (Figure 2A). For Figure 2C, we used 2 WT/HAQ and 3 WT/WT individuals (lines 738-739). We generate HAQ, AQ THP-1 cells in STING-KO THP-1 cells (Invivogen,, cat no. thpd-kostg) (lines 740-741). 

A recent study found that STING agonist SHR1032 induces cell death in STING-KO THP-1 cells expressing WT(R232) human STING 10 (line 182) independent of type I IFNs. SHR1032 suppressed THP1-STING-WT(R232) cell growth at GI50: 23 nM while in the parental THP1STING-HAQ cells, the GI50 of SHR1032 was >103 nM 10. Cytarabine was used as an internal control where SHR1032 killed more robustly than cytarabine in the THP1-STING-WT(R232) cells but much less efficiently than cytarabine in the THP-1-STING-HAQ cells 10.   

This manuscript rigorously uses mouse splenocytes, human lung lymphocytes, THP-1 reconstituted with HAQ, AQ, and HAQ/SAVI, AQ/SAVI mice, to demonstrate that the common human HAQ, AQ alleles are resistant to STING cell death in vitro and in vivo.

We agree with reviewer 1 that STING-mediated cell death mechanisms in myeloid and lymphoid cells may be different and likely contribute to the different mechanisms proposed in STING cell death research 7,9,10. Our study focuses on the in vivo mechanism of T cellpenia.  

Responses to Comment 5: We stated in the Introduction that “AQ responds to CDNs and produce type I IFNs in vivo and in vitro 3,13,14 ”(line 94, 95). We reported that the AQ knock in mice responded to STING activation 3. We previously showed that there was a negative natural selection on the AQ allele in individuals outside of Africa 3. 28% of Africans are WT/AQ but only 0.6% East Asians are WT/AQ 3. Future research on the AQ allele will address this interesting question that may shed new mechanistic light on STING action.

Responses to Comment 6: The comment here is similar to comment 3. In this manuscript, Figure 6 shows AQ/SAVI had more T-regs than HAQ/SAVI (lines 246 – 256). In our previous publication on HAQ, AQ knockin mice, we showed that AQ T-regs have more IL-10 and mitochondria activity than HAQ T-regs 3. We propose that increased IL-10+ Tregs in AQ mice may contribute to an improved phenotype in AQ/SAVI compared to HAQ/SAVI. However, we are not excluding other contributions (e.g. metabolic difference) by the AQ allele.

Responses to Comment 7: Both radioresistant parenchymal and/or stromal cells and hematopoietic cells influence SAVI pathology in mice 15,16. Nevertheless, the lack of CD 4 T cells, including the anti-inflammatory T-regs, likely contributes to the inflammation in SAVI mice and patients. We characterized lung function, lung inflammation (Figure 4), lung neutrophils, and inflammatory monocyte infiltration (Figure S4). 

Responses to Comment 8: Several publications have linked STING to HIV pathogenesis 17-22  (line 271). The manuscript studies STING activation-induced cell death. It is not stretching to ask, for example, does preventing STING cell death, without affecting type I IFNs production, restore CD4 T cell counts and improve care for AIDS patients?

Reviewer #2 (Public Review):

Response to Comment 1: Please see the Figure below for cell death by diABZI, DMXAA in Splenocytes from WT/WT, WT/HAQ, HAQ/SAVI, AQ/SAVI mice. The HAQ/SAVI and AQ/SAVI splenocytes showed similar partial resistance to STING activationinduced cell death. 

Responses to Comment 2: We examined HAQ, AQ mouse splenocytes, HAQ human lung lymphocytes, THP-1 reconstituted with HAQ, AQ, and HAQ/SAVI, AQ/SAVI mice, to demonstrate that the common human HAQ, AQ alleles are resistant to STING cell death in vitro and in vivo. Additional human T cell line work does not add too much. 

Responses to Comment 3: This is possibly a misunderstanding. We use BMDM for the purpose of comparing STING signaling (TBK1, IRF3, NFκB, STING activation) by WT/SAVI, HAQ/SAVI, AQ/SAVI. Ideally, we would like to compare STING signaling in CD4 T cells from WT/SAVI to HAQ/SAVI, AQ/SAVI mice. However, WT/SAVI has no CD4 T cells. Here, we are making the assumption that the basic STING signaling (TBK1, IRF3, NFκB, STING activation) is conserved between T cells and macrophages. 

Responses to Comment 4: Reviewer 2 suggests looking for evidence of inflammation and STING activation in the lungs of HAQ/SAVI, AQ/SAVI. We would like to elaborate further. First, anti-inflammatory treatments, e.g. steroids, DMARDs, IVIG, Etanercept, rituximab, Nifedipine, amlodipine, et al., all failed in SAVI patients 11. Second, Figure S4 examined lung neutrophils and inflammatory monocyte infiltration. Interestingly, while AQ/SAVI mice had a better lung function than HAQ/SAVI mice (Figure 4D, 4E vs 4H, 4I), HAQ/SAVI and AQ/SAVI lungs had comparable neutrophils and inflammatory monocyte infiltration. Last, SAVI is classified as type I interferonopathy 11, but the lung diseases of SAVI are mainly independent of type I IFNs 23-26. The AQ allele suppresses SAVI in vivo.  Understanding the mechanisms by which AQ rescues SAVI can generate curative care for SAVI patients.  

Author response image 1.

(A-B). Flow cytometry of HAQ/SAVI, AQ/SAVI, WT/WT or WT/HAQ splenocytes treated with diABZI (100ng/ml) or DMXAA (20µg/ml) for 24hrs. Cell death was determined by PI staining. Data are representative of three independent experiments. Graphs represent the mean with error bars indication s.e.m. p values are determined by one-way ANOVA Tukey’s multiple comparison test. * p<0.05. n.s: not significant.

References.

(1)             Patel, S. et al. The Common R71H-G230A-R293Q Human TMEM173 Is a Null Allele. J Immunol 198, 776-787 (2017). 

(2)             Sebastian, M. et al. Obesity and STING1 genotype associate with 23-valent pneumococcal vaccination efficacy. JCI Insight 5 (2020). 

(3)             Mansouri, S. et al. MPYS Modulates Fatty Acid Metabolism and Immune Tolerance at Homeostasis Independent of Type I IFNs. J Immunol 209, 2114-2132 (2022). 

(4)             Sivick, K. E. et al. Comment on "The Common R71H-G230A-R293Q Human TMEM173 Is a Null Allele". J Immunol 198, 4183-4185 (2017). 

(5)             Gulen, M. F. et al. Signalling strength determines proapoptotic functions of STING. Nat Commun 8, 427 (2017). 

(6)             Kabelitz, D. et al. Signal strength of STING activation determines cytokine plasticity and cell death in human monocytes. Sci Rep 12, 17827 (2022). 

(7)             Murthy, A. M. V., Robinson, N. & Kumar, S. Crosstalk between cGAS-STING signaling and cell death. Cell Death Differ 27, 2989-3003 (2020). 

(8)             Kuhl, N. et al. STING agonism turns human T cells into interferon-producing cells but impedes their functionality. EMBO Rep 24, e55536 (2023). 

(9)             Li, C., Liu, J., Hou, W., Kang, R. & Tang, D. STING1 Promotes Ferroptosis Through MFN1/2-Dependent Mitochondrial Fusion. Front Cell Dev Biol 9, 698679 (2021). 

(10)         Song, C. et al. SHR1032, a novel STING agonist, stimulates anti-tumor immunity and directly induces AML apoptosis. Sci Rep 12, 8579 (2022). 

(11)         Liu, Y. et al. Activated STING in a vascular and pulmonary syndrome. N Engl J Med 371, 507-518 (2014). 

(12)         Jin, L. et al. Identification and characterization of a loss-of-function human MPYS variant. Genes Immun 12, 263-269 (2011). 

(13)         Yi, G. et al. Single nucleotide polymorphisms of human STING can affect innate immune response to cyclic dinucleotides. PLoS One 8, e77846 (2013). 

(14)         Patel, S. et al. Response to Comment on "The Common R71H-G230A-R293Q Human TMEM173 Is a Null Allele". J Immunol 198, 4185-4188 (2017). 

(15)         Gao, K. M. et al. Endothelial cell expression of a STING gain-of-function mutation initiates pulmonary lymphocytic infiltration. Cell Rep 43, 114114 (2024). 

(16)         Gao, K. M., Motwani, M., Tedder, T., Marshak-Rothstein, A. & Fitzgerald, K. A. Radioresistant cells initiate lymphocyte-dependent lung inflammation and IFNgammadependent mortality in STING gain-of-function mice. Proc Natl Acad Sci U S A 119, e2202327119 (2022). 

(17)         Monroe, K. M. et al. IFI16 DNA sensor is required for death of lymphoid CD4 T cells abortively infected with HIV. Science 343, 428-432 (2014). 

(18)         Doitsh, G. et al. Cell death by pyroptosis drives CD4 T-cell depletion in HIV-1 infection. Nature 505, 509-514 (2014). 

(19)         Jakobsen, M. R., Olagnier, D. & Hiscott, J. Innate immune sensing of HIV-1 infection. Curr Opin HIV AIDS 10, 96-102 (2015). 

(20)         Silvin, A. & Manel, N. Innate immune sensing of HIV infection. Curr Opin Immunol 32, 54-60 (2015). 

(21)         Altfeld, M. & Gale, M., Jr. Innate immunity against HIV-1 infection. Nat Immunol 16, 554-562 (2015). 

(22)         Krapp, C., Jonsson, K. & Jakobsen, M. R. STING dependent sensing - Does HIV actually care? Cytokine Growth Factor Rev 40, 68-76 (2018). 

(23)         Luksch, H. et al. STING-associated lung disease in mice relies on T cells but not type I interferon. J Allergy Clin Immunol 144, 254-266 e258 (2019). 

(24)         Stinson, W. A. et al. The IFN-gamma receptor promotes immune dysregulation and disease in STING gain-of-function mice. JCI Insight 7 (2022). 

(25)         Warner, J. D. et al. STING-associated vasculopathy develops independently of IRF3 in mice. J Exp Med 214, 3279-3292 (2017). 

(26)         Fremond, M. L. et al. Overview of STING-Associated Vasculopathy with Onset in Infancy (SAVI) Among 21 Patients. J Allergy Clin Immunol Pract 9, 803-818 e811 (2021).

Author response:

eLife assessment

This valuable study reveals how a rhizobial effector protein cleaves and inhibits a key plant receptor for symbiosis signaling, while the host plant counters by phosphorylating the effector. The molecular evidence for the protein-protein interaction and modification is solid, though biological evidence directly linking effector cleavage to rhizobial infection is incomplete. With additional functional data, this work could have implications for understanding intricate plant-microbe dynamics during mutualistic interactions.

Thank you for this helpful comment. In the revised manuscript version, we will be more prudent with directly linking cleavage of Nod factor receptors by NopT and rhizobial infection.

We plan to modify the Title, the One-Sentence Summary, Abstract, and Discussion regarding this point.

Public Reviews:

Reviewer #1 (Public Review):

Bacterial effectors that interfere with the inner molecular workings of eukaryotic host cells are of great biological significance across disciplines. On the one hand they help us to understand the molecular strategies that bacteria use to manipulate host cells. On the other hand they can be used as research tools to reveal molecular details of the intricate workings of the host machinery that is relevant for the interaction/defence/symbiosis with bacteria. The authors investigate the function and biological impact of a rhizobial effector that interacts with and modifies, and curiously is modified by, legume receptors essential for symbiosis. The molecular analysis revealed a bacterial effector that cleaves a plant symbiosis signaling receptor to inhibit signaling and the host counterplay by phosphorylation via a receptor kinase. These findings have potential implications beyond bacterial interactions with plants.

Thank you for highlighting the broad significance of rhizobial effectors in understanding legume-rhizobium interactions. We fully agree with your assessment and will emphasize these points in the revised Introduction and Discussion sections of our manuscript. Specifically, we will expand our Discussion regarding the potential impact of the NopT interaction with symbiotic receptor kinases on plant immune signaling and regarding the general significance of our work.

Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis. A rhizobial effector is described to directly modify symbiosis-related signaling proteins, altering the outcome of the symbiosis. Overall, the paper presents findings that will have a wide appeal beyond its primary field.

Out of 15 identified effectors from Sinorhizobium fredii, they focus on the effector NopT, which exhibits proteolytic activity and may therefore cleave specific target proteins of the host plant. They focus on two Nod factor receptors of the legume Lotus japonicus, NFR1 and NFR5, both of which were previously found to be essential for the perception of rhizobial nod factor, and the induction of symbiotic responses such as bacterial infection thread formation in root hairs and root nodule development (Madsen et al., 2003, Nature; Tirichine et al., 2003; Nature). The authors present evidence for an interaction of NopT with NFR1 and NFR5. The paper aims to characterize the biochemical and functional consequences of these interactions and the phenotype that arises when the effector is mutated.

Thank you for your positive feedback on our manuscript. In the revised Introduction and Discussion sections, we plan to better emphasize the interdisciplinary significance of our work. We will show how the knowledge gained from our study can contribute to a better understanding of microbial interactions with eukaryotic hosts in general, which may have a stimulating effect on future research in various research areas such as pathogenesis and immunity.

To ensure that the readers can easily follow the rationale behind our experiments, we will improve the Results section and provide more detailed explanations of how NopT among 15 examined effectors was selected. Additionally, we will provide more background information on NopT and the roles of NFR1 and NFR5 in symbiotic signaling in the Introduction section. As suggested, we will include the references Madsen et al. (2003) and Tirichine et al. (2003) as well as additional references on rhizobial NopT proteins into our revised manuscript version.

Evidence is presented that in vitro NopT can cleave NFR5 at its juxtamembrane region. NFR5 appears also to be cleaved in vivo. and NFR1 appears to inhibit the proteolytic activity of NopT by phosphorylating NopT. When NFR5 and NFR1 are ectopically over-expressed in leaves of the non-legume Nicotiana benthamiana, they induce cell death (Madsen et al., 2011, Plant Journal). Bao et al., found that this cell death response is inhibited by the coexpression of nopT. Mutation of nopT alters the outcome of rhizobial infection in L. japonicus. These conclusions are well supported by the data.

We appreciate that you recognize the value of our data.

The authors present evidence supporting the interaction of NopT with NFR1 and NFR5. In particular, there is solid support for cleavage of NFR5 by NopT (Figure 3) and the identification of NopT phosphorylation sites that inhibit its proteolytic activity (Figure 4C). Cleavage of NFR5 upon expression in N. benthamiana (Figure 3A) requires appropriate controls (inactive mutant versions) that have been provided, since Agrobacterium as a closely rhizobia-related bacterium, might increase defense related proteolytic activity in the plant host cells.

Thank you for recognizing the use of an inactive NopT variant in Figure 3A. In fact, increased activity of plant proteases induced by Agrobacterium is an important point that should not be neglected. We plan to mention this aspect in our revised Discussion.

In the context of your comments, we are planning to make the following improvements to the manuscript:

(1) We will add a more detailed description of the experimental conditions under which the cleavage of NFR5 by NopT was observed in vitro and in vivo.

(2) We plan to provide more comprehensive data on the phosphorylation of NopT by NFR1, including phosphorylation assays and mass spectrometry results. These additional data support the proposed mechanism by which NFR1 inhibits the proteolytic activity of NopT.

(3) We will expand the Discussion on the cell death response induced by ectopic expression of NFR1 and NFR5 in Nicotiana benthamiana. We will include more details from Madsen et al. (2011) to contextualize our findings with published literature.

We believe these additions and clarifications will enhance the clarity and impact of our findings.

Key results from N. benthamiana appear consistent with data from recombinant protein expression in bacteria. For the analysis in the host legume L. japonicus transgenic hairy roots were included. To demonstrate that the cleavage of NFR5 occurs during the interaction in plant cells the authors build largely on western blots. Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with nopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). It is not quite clear how the authors explain the loss of NFR5 function (loss of cell death, impact on symbiosis), as a vast excess of the tested target remains intact. It is also not clear why a large proportion of NFR5 is unaffected by the proteolytic activity of NopT. This is particularly interesting in Nicotiana in the absence of Nod factor that could trigger NFR1 kinase activity.

Thank you for your comments regarding the cleavage of NFR5 and its functional implications. In the revised version, we will change our manuscript taking into account the following considerations:

(1) We acknowledge that the Western blots indicate only a small proportion of NFR5 is cleaved when co-expressed with NopT. It is worth noting in this context that the proteins were expressed at high levels which likely do not reflect the natural situation in L. japonicus. Low production of cleaved NFR5 in our Western blots with transformed N. benthamiana or L. japonicus cells thus may simply reflect an experimental effect due to high NFR5 protein synthesis. We suggest that the presence of high amounts of intact NFR5 does not have a significant functional impact on plant responses (cell death in N. benthamiana, rhizobial infection of L. japonicus) whereas NFR5 cleavage (or formation of NFR5 cleavage products) may be crucial for the observation of the observed phenotypic changes. The fraction of cleaved NFR5, although small, may be sufficient to disrupt crucial signaling pathways, leading to observable phenotypic changes. We will address possible differences between experimental and natural protein levels in our revised Discussion.

(2) We studied in our work three biochemical aspects of NopT: (i) physical binding of NopT to NFR1 and NFR5 (ii) proteolytical cleavage of NFR5 by NopT and (iii) phosphorylation of NopT by NFR1. These three biochemical properties appear to influence each other. Phosphorylation of NopT by NFR1 appears to reduce its proteolytic activity, thereby counteracting NFR5 degradation by NopT (NFR5 homeostasis). Moreover, as NopT is a phosphorylation substrate for NFR1, NopT probably interferes with kinase mediated downstream responses of NFR1. Thus, NFR5 cleavage activity of NopT appears to be only one feature of NopT. We plan to mention these considerations in our revised Discussion.

It is also difficult to evaluate how the ratios of cleaved and full-length protein change when different versions of NopT are present without a quantification of band strengths normalized to loading controls (Figure 3C, 3D, 3F). The same is true for the blots supporting NFR1 phosphorylation of NopT (Figure 4A).

Thank you for pointing out this aspect. Following your recommendation, we will quantify the band intensities for cleaved and full-length NFR5 in the experiments with different versions of NopT. These values will be normalized to loading controls. Similarly, the Western blots supporting NFR1 phosphorylation of NopT will be quantified. The data for normalized band intensities will be included into the revised figures. The quantifications will provide a clearer understanding of how the ratios of cleaved to full-length proteins change with different NopT variants and also will provide information to which extent NopT is phosphorylated by NFR1.

It is clear that mutation of nopT results in a quantitative infection phenotype. Nodule primordia and infection threads are still formed when L. japonicus plants are inoculated with ∆nopT mutant bacteria, but it is not clear if these primordia are infected or develop into fully functional nodules (Figure 5). A quantification of the ratio of infected and non-infected nodules and primordia would reveal whether NopT is only active at the transition from infection focus to thread or perhaps also later in the bacterial infection process of the developing root nodule.

Thank you for pointing this out. In the revised version of our manuscript, we will provide data showing that there are no obvious differences in nodule formation in plants inoculated with ∆nopT and wild-type NGR234, respectively. However, quantification of infection threads containing our GFP-labeled rhizobia in primordia and nodules would be difficult to perform due to strong autofluorescence signals in these tissues. The main goal of our study was to identify and characterize the interaction between NopT and Nod factor receptors. We therefore believe that an in-depth analysis of the bacterial infection process at later symbiotic stages is out of the scope of the present work.

Reviewer #2 (Public Review):

Summary:

This manuscript presents data demonstrating NopT's interaction with Nod Factor Receptors NFR1 and NFR5 and its impact on cell death inhibition and rhizobial infection. The identification of a truncated NopT variant in certain Sinorhizobium species adds an interesting dimension to the study. These data try to bridge the gaps between classical Nod-factor-dependent nodulation and T3SS NopT effector-dependent nodulation in legume-rhizobium symbiosis. Overall, the research provides interesting insights into the molecular mechanisms underlying symbiotic interactions between rhizobia and legumes.

Strengths:

The manuscript nicely demonstrates NopT's proteolytic cleavage of NFR5, regulated by NFR1 phosphorylation, promoting rhizobial infection in L. japonicus. Intriguingly, authors also identify a truncated NopT variant in certain Sinorhizobium species, maintaining NFR5 cleavage but lacking NFR1 interaction. These findings bridge the T3SS effector with the classical Nod-factor-dependent nodulation pathway, offering novel insights into symbiotic interactions.

We appreciate that you recognize the value of our manuscript.

Weaknesses:

(1) In the previous study, when transiently expressed NopT alone in Nicotiana tobacco plants, proteolytically active NopT elicited a rapid hypersensitive reaction. However, this phenotype was not observed when expressing the same NopT in Nicotiana benthamiana (Figure 1A). Conversely, cell death and a hypersensitive reaction were observed in Figure S8. This raises questions about the suitability of the exogenous expression system for studying NopT proteolysis specificity.

We appreciate your attention to these plant-specific differences. In view of your comments, we plan to revise the Discussion and explain the different expression systems used for studying NopT effects in planta. Previous studies showed that NopT expressed in tobacco (N. tabacum) or in specific Arabidopsis thaliana ecotypes (with PBS1/RPS5 genes) causes rapid cell death (Dai et al. 2008; Khan et al. 2022). Our data shown in Fig. S8 confirm these findings. As cell death (effector triggered immunity) is usually associated with induction of protease activities, we considered N. tabacum and A. thaliana plants as not suitable for testing NFR5 cleavage by NopT. In fact, no NopT/NFR5 experiments were performed with these plants in our study. In contrast, the expression of NopT in Nicotiana benthamiana did not lead to cell death in our experiments. Khan et al. 2022 also reported that cell death does not occur in N. benthamiana unless the cells were transformed with PBS1/RPS5 constructs. Thus, N. benthamiana is a suitable expression system to analyze NopT protease activity on co-expressed substrates. Our revision aims to better understand the advantages of the N. benthamiana expression system for studying NopT mediated proteolysis of NFR5.

(2) NFR5 Loss-of-function mutants do not produce nodules in the presence of rhizobia in lotus roots, and overexpression of NFR1 and NFR5 produces spontaneous nodules. In this regard, if the direct proteolysis target of NopT is NFR5, one could expect the NGR234's infection will not be very successful because of the Native NopT's specific proteolysis function of NFR5 and NFR1. Conversely, in Figure 5, authors observed the different results.

Our inoculation experiments clearly show that NopT of NGR234 has a negative effect on formation of infection foci (Fig. 5A) and nodule primordia (Fig. 5E). Our biochemical analysis indicates that NopT targets the NFR1/NFR5 complex, which most likely impairs activation of downstream responses such as NIN gene expression. Accordingly, NIN promoter activity was found to be higher in roots inoculated with the Δ_nopT_ mutant as compared to the NGR234 wild-type (Fig. 5B and 5D). It is therefore plausible that NopT impairs rhizobial infection of L. japonicus due to inhibition of NFR1/NFR5 functions. We agree with this Reviewer that it can be expected that “NGR234's infection will not be very successful”. Fig. 5 confirms that Δ_nopT_ mutant is indeed a better symbiont and we do not think that we obtained “unexpectedly different results”. In the revised version, we will try to formulate our discussion text better in order to avoid any misunderstandings. Furthermore, will write as figure title “NopT dampens rhizobial infection…” instead of “NopT regulates rhizobial infection…”. We are also considering changing the title of our manuscript.  

(3) In Figure 6E, the model illustrates how NopT digests NFR5 to regulate rhizobia infection. However, it raises the question of whether it is reasonable for NGR234 to produce an effector that restricts its own colonization in host plants.

We acknowledge the potential paradox of NGR234 producing an effector that appears to restrict its own colonization in host plants. In fact, depending on the host plant, most rhizobial effectors are “double-edged swords” that play either a positive or negative role in the symbiosis. In response to your comment, we will discuss the possibility that NopT may confer selective advantages in interactions between NGR234 and host plants where NopT plays a positive symbiotic role (Dai et al. 2008; Kambara et al. 2009). Inhibition of NFR1/NFR5 functions by NopT in these host plants could be a feedback response in cells in which symbiotic signaling has already started. It is tempting speculate that the interaction between NopT and Nod factor receptors reduces Nod factor perception and downstream signaling to avoid a possible overreaction of symbiotic signaling, which may result in hypernodulation or formation of empty nodules without bacteria. Furthermore, it is tempting to speculate that NopT targets not only Nod factor receptors but also other host proteins to promote symbiosis, e.g. by suppressing excessive immune responses triggered by hyperinfection of rhizobia. In our revised manuscript, we will highlight the need for further investigations to elucidate the precise mechanisms underlying the observed infection phenotype and the role of NopT in modulating symbiotic signaling pathways.  

(4) The failure to generate stable transgenic plants expressing NopT in Lotus japonicus is surprising, considering the manuscript's claim that NopT specifically proteolyzes NFR5, a major player in the response to nodule symbiosis, without being essential for plant development.

Thank you for your comments. The failure to obtain L. japonicus plants constitutively expressing NopT was indeed surprising and suggests that NopT targets not only NFR5 but also other proteins in L. japonicus. The number of NopT substrates in plants could be greater than assumed. For example, we show in our work that NopT can cleave AtLYK5 and LjLYS11. In our manuscript, we don’t provide protocols and data on our efforts to construct L. japonicus plants stably expressing NopT. Indeed, it cannot be completely ruled out that the observed failure is not due to NopT expression, but rather to other factors that influence the transformation and regeneration of explants into whole plants. Our results should therefore not be over-interpreted. We consider a discussion of our failed transformation experiments to be somewhat preliminary and not central to this manuscript. herefore, we plan to modify our Discussion and delete the sentence reporting that stable transgenic plants expressing NopT have not been successfully generated.

Author response:

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

We thank the reviewers for their overall careful evaluation of our work, the constructive criticism, and their many helpful suggestions. We feel that our revision built on the strengths identified by the reviewers, and addressed all the concerns they have raised. Both reviewers recognize that our revisions have improved the paper.  Since the first submission we have:

• Rewritten large parts of the papers to improve clarity and make it more concise where possible

• Simulated an alternative working memory model, as recommended by Reviewer 1

• Included 4 new/revised supplementary figures, following the reviewer’s suggestions for additional analysis.

Below we provide a brief response to the Reviewers’ comments on our manuscript revision.

Reviewer #1: Public Review:

Strengths:

Overall, the work offers a very interesting approach of a topic which is hard to accomplish experimentally --therefore the computational take is entirely justified and extremely useful. The authors carefully designed the computational experiments to shed light into the demyelination effects on working memory from multiple levels of description, increasing the reliability of their conclusions. I think this work provides now convincing evidence and has the potential to be influential in future studies of myelin alterations (and related disorders such as multiple sclerosis).

Weaknesses:

In its current form, the authors have improved the clarity of the results and the model details, and have provided a new set of simulations to complement and reinforce the original ones (including the development of a new spatial working memory model based on silent working memory principles). I do not appreciate any significant weaknesses at this point.

We thank the reviewer for these positive comments on our revision and for the suggestion of adding the silent memory model, as we feel this has strengthened our findings.

Reviewer #2: Public Review:

This paper analyzes the effect of axon de-myelination and re-myelination on action potential speed, and propagation failure. Next, the findings are then incorporated in a standard spiking ring attractor model of working memory.

I think the results are not very surprising or solid and there are issues with method and presentation.

The authors did many simulations with random parameters, then averaged the result, and found for instance that the Conduction Velocity drops in demyelination. It gives the reader little insight into what is really going on. My personal preference is for a well understood simple model rather than a poorly understood complex model. The link between the model outcome of WM and data remains qualitative and is further weakened by the existence of known other age-related effects in PFC circuits.

Comments on revised version:

The paper has improved in the revision, although I still think a reduced model would have been nice.

As noted above, in addition to our spiking bump attractor model, our revision includes a second network-level model:  an activity-silent working memory model for continuous features.  We found qualitatively similar effects as in our bump attractor network model, showing that our main conclusions do not critically depend on the exact working memory mechanism (active vs. activity-silent).  This new model was described in two new supplementary figures and a new paragraph in the Results section.

We did not add a reduced model in our revision to this paper, since neither reviewer explicitly recommended that we add one.  As we noted in our private response to reviewers that accompanied our revision: we share the view that understanding simple models can provide critical insights into brain function (and we believe that many of our papers related to attractor dynamics in working memory and decision-making fall into this category, e.g. Wimmer et al. 2014, Esnaola-Acebes et al. 2022, Ibañez et al 2020). We disagree with the reviewer on an important point: we feel that the model complexity that we have chosen is appropriate and necessary to study the phenomenon at hand. Our modeling efforts are principled, with complexity added as necessary. We started with a biophysical single neuron model with firing dynamics fit to empirical data in pyramidal neurons of rhesus monkey dlPFC (Rumbell et al. 2016) – the same type of neurons and cortical region analyzed in the Peters et al. work on structural changes to myelin seen during aging (e.g., Figure 1).  Because simple models do not accurately capture the CV along thin axons like those in the PFC, we attached a multicompartment axon with detailed myelinated segments, and constructed a cohort of feasible models. We then used this cohort to get quantitative estimates of the effects of variable degrees of demyelination and remyelination. This would not be possible with a simpler model. We then study the consequences of de- and re-myelination in a spiking neural network model. Again, we could not use a simpler model (e.g. a firing rate attractor model) without making gross assumptions about how demyelination affects circuit function. In sum, we believe that our models are relatively simple but comprehensive given the phenomenon that we are studying.

The reviewer is correct in that there exist “known other age-related effects in PFC circuits”. These are reviewed in the introduction and we discuss future extensions of our model that would incorporate those effects as well. It is important to note that this is the first comprehensive study of demyelination effects in aging PFC, demonstrating that myelin changes alone predict working memory changes associated with aging.

While we agree that averaging results about different parameter sets provide a limited understanding of the system, we persist in our belief that such analyses provide an important baseline.  We acknowledge that results vary across our model cohort; this is why we included the heatmaps of our single cell model perturbation results (Figure 3 and Supplementary Figure 3), and simulated network models representing a heterogeneity of neuronal axons with healthy and altered myelin sheaths in different degrees, as likely occurs in the aging brain (Figures 7 and 8).  The model framework we present here is well-suited for more targeted analyses and better insights, including those which we are pursuing currently.

---

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

We thank the reviewers for their careful evaluation of our work, the constructive criticism, and their many helpful suggestions. We feel that our revision builds on the strengths identified by the reviewers, and addresses all the concerns they have raised. We have:

• Rewritten large parts of the papers to improve clarity and make it more concise where possible

• Simulated an alternative working memory model

• Included 4 new/revised supplementary figures, following the reviewer’s suggestions for additional analysis

Reviewer #1 (Public Review):

Summary:

The authors study the effects of myelin alterations in working memory via the complementary use of two computational approaches: one based on the de- and re-myelination in multicompartmental models of pyramidal neurons, and one based on synaptic changes in a spiking bump attractor model for spatial working memory. The first model provides the most precise angle (biophysically speaking) of the different effects (loss of myelin lamella or segments, remyelination with thinner and shorter nodes, etc), while the second model allows to infer the consequences of myelin alterations in working memory performance, including memory stability, duration, and bump diffusion. The results indicate (i) a slowing down and failure of propagation of spikes with demyelination and partial recovery with remyelination, with detailed predictions on the role of nodes and myelina lamella, and (ii) a decrease in memory duration and an increase in memory drift as a function of the demyelination, in agreement with multiple experimental studies.

Strengths:

Overall, the work offers a very interesting approach of a topic which is hard to accomplish experimentally --therefore the computational take is entirely justified and extremely useful. The authors carefully designed the computational experiments to shed light into the demyelination effects on working memory from multiple levels of description, increasing the reliability of their conclusions. I think this work is solid and has the potential to be influential in future studies of myelin alterations (and related disorders such as multiple sclerosis).

We thank the reviewer for these positive comments on our manuscript.

Weaknesses:

In its current form, the study still presents several issues which prevent it from achieving a higher potential impact. These can be summarized in two main items. First, the manuscript is missing some important details about how demyelination and remyelination are incorporated in both models (and what is the connection between both implementations). For example, it is unclear whether an unperturbed axon and a fully remyelinated axon would be mathematically equivalent in the multicompartment model, or how the changes in the number of nodes, myelin lamella, etc, are implemented in the spiking neural network model.

We thank the reviewer for these suggestions to improve the clarity of our manuscript. A ‘fully remyelinated’ axon is not mathematically equivalent to the unperturbed axon: it has shorter and thinner myelinated segments, and additional nodes in between. This is consistent with empirical observations in rhesus monkey dlPFC, as reviewed in Peters et al. (2009): a 90% increase in paranode profiles, and myelin sheaths that were thinner than expected for the size of the enclosed axon. With no empirical observations of fewer numbers of nodes (but rather, the opposite) or bare sections of axon, we assumed that the remyelination process also creates new nodes (which are identical to existing nodes), as also modeled in Scurfield & Latimer (2018). We have added two new sentences to the results to clarify this fact, before presenting the first set of results for the single cell model: (starting at line 137):

“To simulate demyelination, we removed lamellae from selected myelinated segments; for remyelination we replaced a fraction of myelinated segments by two shorter and thinner segments with a node in between. As such, a ‘fully remyelinated axon’ had all the demyelinated segments subsequently remyelinated, but with fewer lamellae and additional nodes compared to the unperturbed control case, consistent with empirical observations (Peters, 2009).”

We also state the maximal amount of remyelination more explicitly in the Results, starting on lines 164-165: "We next examined the extent to which remyelination with shorter and thinner segments, occurring after demyelination, restored axonal AP propagation (Figure 4).”

Also on line 192-193: “Remyelinating all affected segments with 75% of lamellae (the maximal amount of remyelination) nearly eliminated AP failures (1.8 ± 1.1%).”

Finally, in Methods we also clarified the structure of the added node (starting at line 634): “Remyelination was performed by replacing an affected (previously demyelinated) segment with two shorter segments, each including paranodes, juxtaparanodes, and an internode, and a new node between them that was identical to existing nodes.”

We have also provided further details describing how myelin dystrophy was simulated in the network model in Results (lines 243 - 249) and in Methods (lines 722 - 747). How myelin alterations have been implemented in the network model is one of the questions of the reviewer (Question 5 in Reviewer #1: Recommendations for the Authors_)._ We have addressed this question by describing in detail how we adjusted CV and AP failure rate to the values produced by the multicompartment neuron model. Please see our answer to Question 5 for the details.

Second, it is unclear whether some of the conclusions are strong computational predictions or just a consequence of the model chosen. For example, the lack of effect of decreasing the conduction velocity on working memory performance could be due to the choice of considering a certain type of working memory model (continuous attractor), and therefore be absent under other valid assumptions (i.e. a silent working memory model, which has a higher dependence on temporal synaptic dynamics).

Whether some conclusions are strong predictions or just a consequence of the model chosen is an important concern and indeed a general problem of computational modeling of working memory. For example, Stein et al. (Stein et al. Towards biologically constrained attractor models of schizophrenia, Curr. Opin. Neurobiol. 2021) showed that opposed manipulations of E/I ratio can produce the same behavioral pattern in different alternative, plausible biological network models. As long as we do not fully understand the neural mechanisms underlying working memory, modeling studies of how alterations (e.g. in E/I ratio or in the reliability and timing of axonal transmission, as we did here) affect circuit function need to be interpreted critically and tested against new experimental data.

One way to strengthen model predictions is by showing that different computational models make similar predictions. To do this, we implemented an activity-silent working memory model for continuous features, as suggested by the reviewer, and we found qualitatively similar effects as in our bump attractor network model. Thus, our main conclusions do not critically depend on the exact working memory mechanism (active vs. activity-silent).

In the revised manuscript, we have added two new supplementary figures (Supplementary Figure 8 and 9, see the next page) and a new paragraph in the Results section about activity silent working memory (starting at line 319):

“Alternative working memory mechanisms. Working memory in our neural network is maintained in an attractor state with persistent neural activity (Compte et al., 2000; Hansel and Mato, 2013). Other mechanisms have been proposed, including that working memory maintenance may rely on activity-silent memory traces (Mongillo et al., 2008; Stokes, 2015; Barbosa et al., 2020). In activity-silent models, a slowly decaying transient of synaptic efficacy preserves information without the need for persistent ongoing activity. We implemented an activity-silent model, to our knowledge the first one for continuous spatial locations, and tested how working memory performance is affected by AP failures and propagation delays. We found that AP failures corresponding to demyelination caused working memory errors qualitatively similar to the delay-active network (Supplementary Figure 8). On the other hand, increasing propagation delays did not lead to additional working memory errors, unless we include unrealistically high values (uniform distribution in the range of 0 to 100 ms; Supplementary Figure 9). These results are qualitatively similar to the delay active network model. Thus, our main findings do not critically depend on the exact working memory mechanism (active vs. activity-silent).”

Author response image 1.

Action potential failures impair working memory performance in a network model with activity-silent memory traces. (A) Spiking and synaptic activity in an unperturbed, activity-silent working memory model. Top: Raster plot showing the activity for each excitatory neuron (labeled by its preferred direction) in a single trial with a cue stimulus presented at 180°. We modified our spiking neural network model such that it does not show elevated persistent firing throughout the delay period (see Figure 5B for comparison). In particular, we reduced the external background input to excitatory neurons by a factor of 3.61% and we increased the cue stimulus amplitude by 12.5%. Even though spiking activity decays to baseline (close to 0 Hz), a memory trace is imprinted in enhanced synaptic strength due to short-term synaptic facilitation (Mongillo et al., 2008). Selective spiking activity is recovered by a non-selective constant input applied during 300 ms to all excitatory neurons during the two reactivation periods (marked by yellow and green rectangles in the raster plot). The amplitude of the input was 11 mV during the first and 13 mV during the second reactivation period. Reactivation periods are marked in light gray shading in the remaining panels below and the cue period is indicated by dark gray shading. Firing rates (second row), synaptic facilitation variable u (third row), and synaptic depression variable x (bottom row) for the same trial, averaged for 500 neurons around the neuron with 180° as preferred direction (solid lines) and around the neuron with 0° as preferred direction (dashed lines). Note that reactivation recovers the activity bump (C) but also causes elevated firing and subsequent enhancement of synapses at all positions in the networks. (B) Activity in a network with demyelination of 50% of the myelinated segments by removing 60% of the myelin lamellae. AP failures lead to reduced firing rates in the cue and early delay periods and consequently to weaker synaptic enhancement. (C) Average spike counts of the excitatory neurons during the cue period (black lines), and the two reactivation periods indicated in the raster plots in A and B (yellow and green lines). Solid lines correspond to the control network and dashed lines to the perturbed network. (D) Memory strength as a function of time for the control and perturbed networks. (E-F) Trajectories of the bump center (i.e., remembered cue location) read out from the neural activity across the cue and delay periods using a population vector (see Methods). Cue position was 180° in all trials. The perturbed network (F) shows larger working memory errors towards the end of the delay period compared to the control network (E).

Author response image 2.

Effect of propagation delays on control and perturbed activity-silent network models. (A) Memory strength during the whole simulation time for the young, control networks relying on activity-silent working memory (Supplementary Figure 8) with zero propagation delays (blue line), and with propagation delays from a uniform distribution with a range between 0 and 40 ms (yellow line) and between 0 and 100 ms (orange line). (B) Memory strength for perturbed networks when demyelinating 25% of the myelinated segments by removing 50% of the myelin lamellae, without delays (red line), and with uniformly distributed delays between 0 and 40 ms (light gray line) and between 0 and 100 ms (black line). The cue period is indicated by dark gray shading and reactivation periods are marked in light gray. Memory strength was calculated by averaging across 280 trials for one network. Shaded areas indicate SEM for each case. For the young, control networks (A), working memory was not affected by including delays of up to 40 ms. Unrealistically long delays ranging up to 100 ms did cause an impairment (the longest delays found for the most extreme perturbation condition – demyelination of 75% of the segments by removing 100% of the myelin lamellae – were of 49.9 ms on average). When also incorporating AP failures to the networks (B), we observed a similar trend. For this perturbation condition, delays of up to 40 ms were already much larger than the delays quantified in the single neuron model (for the case of 25% of the segments demyelinated by removing 50% of the myelin lamellae, the average delay in the cohort was 3.75 ms).

With additional simulations to address these issues, I consider that the present study would become a convincing milestone in the computational modeling of myelin-related models, and an important study in the field of working memory.

Again, we would like to thank the reviewer for the positive comments. We have addressed all the main issues raised (see below our response to the “recommendations for the authors”).

Reviewer #2 (Public Review):

This paper analyzes the effect of axon de-myelination and re-myelination on action potential speed, and propagation failure. Next, the findings are then incorporated in a standard spiking ring attractor model of working memory.

I think the results are not very surprising or solid and there are issues with method and presentation.

The authors did many simulations with random parameters, then averaged the result, and found for instance that the Conduction Velocity drops in demyelination. It gives the reader little insight into what is really going on. My personal preference is for a well understood simple model rather than a poorly understood complex model. The link between the model outcome of WM and data remains qualitative, and is further weakened by the existence of known other age-related effects in PFC circuits.

We thank the reviewer for the critical assessment of our work. We share the view that understanding simple models can provide critical insights into brain function (and we believe that many of our papers related to attractor dynamics in working memory and decision making fall into this category, e.g. Wimmer et al. 2014, Esnaola-Acebes et al. 2022, Ibañez et al 2020). However, we respectfully disagree with the reviewer on an important point: the model complexity that we have chosen is appropriate and necessary to study the phenomenon at hand. Our modeling efforts are principled, with complexity added as necessary. We started with a biophysical single neuron model with firing dynamics fit to empirical data in pyramidal neurons of rhesus monkey dlPFC (Rumbell et al. 2016) – the same type of neurons and cortical region analyzed in the Peters et al. work on structural changes to myelin seen during aging (e.g., Figure 1). Because simple models do not accurately capture the CV along thin axons like those in the PFC, we attached a multicompartment axon with detailed myelinated segments, and constructed a cohort of feasible models. We then used this cohort to get quantitative estimates of the effects of variable degrees of demyelination and remyelination. This would not be possible with a simpler model. We then study the consequences of de- and re-myelination in a spiking neural network model. Again, we could not use a simpler model (e.g. a firing rate attractor model) without making gross assumptions about how demyelination affects circuit function. In sum, we believe that our models are relatively simple but comprehensive given the phenomenon that we are studying.

The reviewer is correct in that there exist “known other age-related effects in PFC circuits”. These are reviewed in the introduction and we discuss future extensions of our model that would incorporate those effects as well. It is important to note that this is the first comprehensive study of demyelination effects in aging PFC, demonstrating that myelin changes alone predict working memory changes associated with aging.

The specific issues about modeling choices and interpretation of the results are discussed below.

Both for the de/re myelination the spatial patterns are fully random. Why is this justified?

We agree that myelin dystrophy during aging could be non-random, that is, localized to certain regions of an axon. Our collaborators (Drs Jennifer Luebke, Maya Medalla, and Patrick Hof) are currently addressing this question using 3D electron microscopy and immunohistochemistry on axons of individual neurons and their associated myelin, but results are not available yet. Early on in this study we examined how the location of myelin alterations affected AP propagation. Focusing demyelination along a section of axon led to more AP slowing and failure than when spatially randomized. Likewise, remyelination of such spatially localized dystrophy led to greater recovery, as there were fewer transitions between long and short internodes (Supplemental Figure 4). Since otherwise the effects in the localized cases were largely similar to those in the spatially random case (see Author response image 3 below), for brevity in this paper we assumed myelin alterations were randomly distributed. Our next paper, extending this study to collateralized axons and which was presented as a poster at the 2023 Society for Neuroscience meeting, will include an examination of localized myelin dystrophy.

Author response image 3.

Effect of localized myelin alterations on CV change. Myelin alterations were either focused on the third of myelinated segments closest to the initial segment (‘proximally clustered’), the third of myelinated segments furthest from the initial segment (‘distally clustered’), or distributed according to a uniform distribution as in the current study. For demyelination, all lamellae were removed from 25% of myelinated segments (showing mean +/- SEM of all 50 cohort models, 30 randomized trials each). For remyelination, affected segments were replaced by two shorter segments with 75% of the original lamellae thickness and a node in between.

We have added two sentences in Methods to justify this assumption more clearly (line 510): “Evidence suggests that aging affects oligodendrocytes in several ways, including the ability for oligodendrocyte precursor cells to mature (Dimovasili et al., 2022). Knowing that individual oligodendrocytes myelinate axons of many different neurons, but without data quantifying how oligodendrocyte dystrophy affects myelination in individual axons, we assumed that myelin alterations were randomly distributed.”

We have also added a sentence in the Discussion alluding to our upcoming study (line 434): “Our model can also be extended to explore interactions between spatially localized myelin perturbations (such as those seen in multiple sclerosis) and axon collateralization (Sengupta et al., 2023), which would affect the distance-dependence of AP failures.”

Similarly, to model the myelin parameters were drawn from uniform distributions, Table 1 (I guess). Again, why is this reasonable?

The reviewer is correct that our initial Latin hypercube sample generated a uniform distribution. However, parameters of the random sample of models selected as biologically feasible were not uniformly distributed. We have added a new figure (Supplementary Figure 1A) to illustrate the parameter distributions, and have added two sentences in Methods (starting on line 596):

“Of the 1600 simulated models, 138 met these criteria; for the present study, we randomly selected 50 models to comprise the young, control model cohort. Along most dimensions, the chosen cohort was approximately normally distributed (Supplementary Figure 1). The g-ratio (ratio of axon to fiber diameter) among models in the cohort was 0.71 ± 0.02, with total axon lengths of 1.2 ± 0.1 cm.”

Author response image 4.

Distribution of parameters and conduction velocities in the single neuron model cohort. (A) Histograms of axon morphology parameters of models selected for the single neuron cohort. Top: axon diameter: middle, length of unperturbed myelin segments; bottom: total myelin thickness in unperturbed segments, computed as the product of lamella thickness and number of lamellae. (B) Histograms of the CV for the 50 axons of the unperturbed model cohort (top), and representative demyelination and remyelination perturbations: mild demyelination (removing 25% of lamellae from 25% of the myelinated segments, second row); severe demyelination (removing all lamellae from 75% of the myelinated segments, third row); and complete (100%) remyelination (where the demyelinated segments from the third row were remyelinated by two shorter segments with 75% of lamellae). CVs averaged over 30 trials in each case. (C) Changes in CV (measured in %) in response to demyelination and remyelination versus the magnitude of current clamp step (+180, +280, or +380 pA). Shown are mean +/- SEM for demyelinating 50% of myelinated segments (removing all lamellae), and subsequent remyelination of those segments by shorter segments with 75% of lamellae.

The focus of most analysis is on the conduction velocity but in the end, this has no effect on WM, so the discussion of CV remains sterile.

CV delays likely do affect brain functions that rely on neuronal oscillations and synchrony, as mentioned in the Discussion. As such, we feel that our single neuron model results on CV delays as well as AP failures are valuable for the scientific community. Yet, given the results of our network models here, the reviewer has a valid point. We have clarified in the introduction that AP failures but not CV delays affected the network output (line 115):

“Higher degrees of demyelination led to slower propagation and eventual failure of APs along the axons of the multicompartment models. In the network models, an increase in AP failure rate resulted in progressive working memory impairment, whereas slower conduction velocities, in the range observed in the multicompartment models, had a negligible effect.”

We have also revised the single neuron section of the Results throughout, to better highlight the effects of myelin dystrophy on AP failures. Revisions to address this in the demyelination section start on line 148:

“AP propagation was progressively impaired as demyelination increased (Figure 3): CV became slower, eventually leading to AP failure. Removing 25% of lamellae had a negligible effect on CV, regardless of how many segments were affected. However, when all lamellae were removed, CV slowed drastically – by 38 ± 10% even when just 25% of the segments were demyelinated in this way, and 35 ± 13% of APs failed. When 75% of segments lost all their lamellae, CV slowed by 72 ± 8% and 45 ± 13% of APs failed.”

Similiarly, we have added several sentences about AP failures that remain after remyelination of the single neuron model (starting on line 190):

“Results for the percentage of AP failures (Figure 4C,F) were consistent with those for CV recovery. Remyelinating all previously demyelinated segments, even adding just 10% of lamellae, brought AP failure rates down to 14.6 ± 5.1%. Remyelinating all affected segments with 75% of lamellae (the maximal amount of remyelination) nearly eliminated AP failures (1.8 ± 1.1%). Incomplete remyelination, where some segments were still demyelinated, still had relatively high AP failure rates. For example, when one eighth of segments were remyelinated with the maximal amount of lamellae and one eighth were left bare, 25.7 ± 11.5% of APs failed across the cohort (Figure 4C, red dashed line and arrow). AP failure rates were slightly lower when starting with partial demyelination: 10.6 ± 7.6% of APs failed in the analogous paradigm (Figure 4F, red dashed line and arrow). In short: combinations of demyelinated and remyelinated segments often led to sizable CV delays and AP failures.”

The more important effect of de/re myelination is on failure. However, the failure is, AFAIK, just characterized by a constant current injection of 380pA. From Fig 2 it seems however that the first spike is particularly susceptible to failure. In other words, it has not been justified that it is fine to use the failure rates from this artificial protocol in the I&F model. I would expect the temporal current trace to affect whether the propagation fails or not.

In general, we did not find the first spike to be more susceptible to failure than latter spikes; the trace in Figure 2 is a representative snapshot intended to illustrate CV slowdown, AP failure, and recovery. Regarding the constant current injection: while the reviewer is correct that neurons do not receive such inputs in vivo, the applied current injections were designed to match in vitro current clamp protocols for these rhesus monkey neurons. While our future studies will include responses to more realistic synaptic inputs, we focused on somatic current injections here. We have added a new panel (C) to Supplementary Figure 1 (see previous response above) showing that the current step magnitude had little effect on the CV change after myelin perturbations; there was little effect on AP failure rates too. We now also state this finding more explicitly in Methods (starting on line 561):

“As done during in vitro electrophysiological experiments (Chang et al., 2005; Ibanez et al., 2020) and past modeling studies (Coskren et al., 2015; Rumbell et al., 2016), we first applied a holding current to stabilize the somatic membrane potential at -70 mV, then injected a current step into the somatic compartment for 2 seconds. …The CV changes in response to myelin alterations were relatively insensitive to variations in the magnitude of suprathreshold somatic current steps (Supplementary Figure 1C), and whether the current was constant or included Gaussian noise. Therefore, here we quantified CV changes and AP failures from responses to constant +380 pA current steps only.”

I don't know if there are many axon-collaterals in the WM circuits and or distance dependence in the connectivity, but if so, then the current implementation of failure would be questionable.

We agree that axon collaterals may affect our results; our unpublished morphological analyses of individual neuron axons indicate that there is a high degree of local axon collateralization in Layer 3 pyramidal neurons in LPFC. In this first study from our group on myelin perturbations, we chose to focus here on unbranched axons. There was some distance dependence of AP failure along the length of the axon. For example, in our most extreme demyelination case (75% of segments losing all their lamellae), about 14% of the axons showed more AP failure at their distal ends relative to the middle (mean difference 6.33%). We are examining this distance dependence more broadly in our next study, now cited in the Discussion (line 434): “Our model can also be extended to explore interactions between spatially localized myelin perturbations (such as those seen in multiple sclerosis) and axon collateralization (Sengupta et al., 2023), which would affect the distance-dependence of AP failures.”

I would also advise against thresholding at 75% failure in Fig3C. Why don't the authors not simply plot the failure rate?

We thank the reviewer for this suggestion, and have made this change. As suggested by the reviewer, we now show the AP failure rate in Figure 3 and Figure 4. The trends shown are nearly identical to those from the high failure trials.

Regarding the presentation, there are a number of dead-end results that are not used further on. The paper is rather extensive, and it would be clearer if written up in half the space. In addition, much information is really supplementary. The issue of the CV I already mentioned, also the Lasso regression for instance remains unused.

We understand the reviewer’s perspective, and we do value brevity when possible. During the revision process we examined the paper carefully, and made things more concise when it was feasible. As mentioned above, reporting CV results is important, though these revisions increased emphasis on results for AP failures in our revision. We combined the two Supplementary Figures about remyelination in the single neuron model into one (Supplementary Figure 3). We also moved the Lasso figure and associated methods to the Supplementary Material (Supplementary Figure 2), and have separated the Lasso results for demyelination and remyelination into their respective paragraphs (lines 154-160 and lines 200-204 respectively). While we do not use the Lasso explicitly later in Results, we cite them in the Discussion when comparing our findings to previous work (starting on line 417):

“Since our single neuron cohort sampled a wide range of parameter space, we used Lasso regression to identify which of the complex, interacting parameters contributed most to CV delays (which preceded AP failures). Parameters including axon diameter, node length, length of myelinated segments, and nodal ion channel densities predicted how our models responded to demyelination and remyelination; these findings are consistent with past modeling studies over more limited parameter ranges (e.g., Goldman and Albus, 1968; Moore et al., 1978; Babbs and Shi, 2013; Young et al., 2013; Schmidt and Knösche, 2019).”

We hope that our revision has struck an appropriate balance between clear and concise writing, and addressing concerns from both reviewers. We greatly value the time you have given to help us to improve our manuscript.

Response to Recommendations for the Authors:

Reviewer #1 (Recommendations for the Authors):

As I mentioned above, I consider that this study is well designed and it offers very interesting results. I have detailed below some of the issues that should be addressed to improve its potential impact in the field:

(1) Across the manuscript, it is not entirely clear how the results of the multicompartmental model compare to existing modeling results on demyelination and CV changes (such as in the papers cited by the authors). Is this section confirming previous results with a new (more accurate) computational model, or are there any new insights previously unreported? A new paragraph in the Discussion putting these results in context would be very useful for the reader.

We thank the reviewer for this suggestion. We have added two new subheadings to organize the Discussion better, and have expanded the single neuron section to three paragraphs. We feel this now clarifies how our model fits in with previous work while stating its novelty more explicitly. Starting on line 391:

“Myelin changes affect AP propagation in a cohort of model neurons

The novelty of our neuron model lies in its systematic exploration of a combination of different myelin perturbation types known to occur in myelin dystrophies, across a wide range of biologically feasible models. Our single neuron model assumed that age-related myelin dystrophies (e.g., Figure 1) alter the insulative properties of lamellae analogously to demyelination, and examined interactions between demyelination and remyelination. Past studies of myelin dystrophy examined how either demyelination or remyelination of all segments affected AP propagation for a few representative axon morphologies. For example, Scurfield and Latimer (2018) explored how remyelination affected CV delays, finding that axons with more transitions between long and short myelinated segments had slower CV (Supplementary Figure 4), and was first to explore how remyelination interacts with tight junctions. However, their study did not couple remyelination and demyelination together or examine AP failures. Other basic findings from our single neuron cohort are consistent with past modeling studies, including that demyelination caused CV slowing and eventual AP failures (Stephanova et al., 2005; Stephanova and Daskalova, 2008; Naud and Longtin, 2019), and, separately, that remyelination with shorter and thinner myelinated segments led to CV slowing (Lasiene et al., 2008; Powers et al., 2012; Scurfield and Latimer, 2018). However, by assuming that some previously demyelinated segments were remyelinated while others were not, we found that models could have much higher AP failure rates than previously reported. Such a scenario, in which individual axons have some segments that are normal, some demyelinated, and some remyelinated, is likely to occur. We also found a few neurons in our cohort showing a CV increase after remyelination, which has not generally been reported before and is likely due to an interplay between ion channels in the new nodes and altered electrotonic lengths in the perturbed myelinated segments (e.g., Waxman, 1978; Naud and Longtin, 2019).

Since our single neuron cohort sampled a wide range of parameter space, we used Lasso regression to identify which of the complex, interacting parameters contributed most to CV delays (which preceded AP failures). Parameters including axon diameter, node length, length of myelinated segments, and nodal ion channel densities predicted how our models responded to demyelination and remyelination; these findings are consistent with past modeling studies over more limited parameter ranges (e.g., Goldman and Albus, 1968; Moore et al., 1978; Babbs and Shi, 2013; Young et al., 2013; Schmidt and Knösche, 2019). Better empirical measurements of these parameters in monkey dlPFC, for example from 3-dimensional electron microscopy studies or single neuron axon studies combined with markers for myelin, would help predict the extent to which myelin dystrophy and remyelination along individual axons with aging affect AP propagation.

Another important feature of our multicompartment model is that it was constrained by morphologic and physiological data in rhesus monkey dlPFC —an extremely valuable dataset from an animal model with many similarities to humans (Upright and Baxter, 2021; Tarantal et al., 2022). While beyond the scope of the current study, this computational infrastructure –with a detailed axon, initial segment, soma, and apical and basal dendrites– enables simultaneous investigations of signal propagation through the dendritic arbor and axon. Our model can also be extended to explore interactions between spatially localized myelin perturbations (such as those seen in multiple sclerosis) and axon collateralization (Sengupta et al., 2023), which would affect the distance-dependence of AP failures. Integrating such results from single neuron models into network models of working memory, as we have done here, is a powerful way to connect empirical data across multiple scales.”

(2) Although the authors provide a well-designed study for the multi-compartmental model, it would be useful to add more details about how an unperturbed model and a completely remyelinated model differ in practice, perhaps right before the first results on the single cell model are presented. Are the new myelin sheaths covering the same % of axon as in the original case? Are there the same number of nodes? It is hard to distinguish which of these results are due to a compensation by the new myelin sheaths and which ones are just the model coming back to its original (and mathematically equivalent) starting point.

A ‘fully remyelinated’ axon is not mathematically equivalent to the unperturbed axon. Newly remyelinated segments had at most 75% of the original number of myelin wraps, with a new node in between, consistent with empirical observations in rhesus monkey dlPFC. Our manuscript changes in response to this recommendation are described in detail above in our response to the public review of the same reviewer.

(3) The authors observe a directed component in the bias that is known to be caused by heterogeneities in network connectivity, as stated in the text. It occurs to me that similar effects could be also caused by an heterogeneous demyelination in parts of the network. Inducing these biases could be another potential effect of demyelination in practice, and could be easily revealed by the author's current model (and displayed in a supplementary figure).

As suggested by the reviewer, we have tested heterogeneous demyelination in parts of the network and the results confirm the reviewer’s intuition. We have included these new results as new Supplementary Figure 7 (see below) and we have added the following sentences in the Legend of Figure 5, line 1265: “When demyelination is restricted to a part of the network, diffusion only increases in the perturbed zone (Supplementary Figure 7).” and in the Discussion (line 457): “In addition to age-related changes in memory duration and precision, our network model predicts an age-related increase in systematic errors (bias) due to an increased drift of the activity bump (Supplementary Figure 11). Moreover, if demyelination is spatially localized in a part of the network, the model predicts a repulsive bias away from the memories encoded in the affected zone (Supplementary Figure 7).”

Author response image 5.

Effect of spatially heterogeneous demyelination of the model neurons according to their preferred angle. We also tested working memory performance in the network when demyelination affects only parts of the network. The figure shows the decoded bump center position during the cue and delay period for the eight possible cue directions when a fraction of neurons was perturbed and the rest of the neurons in the circuit were unaltered (Figure 5B). We perturbed 10% of the neurons around the neuron with preferred direction 90° (left panel), 25% of the neurons around -90° (middle panel), and 50% of the neurons around 180° (right panel). Bump traces for cues that lie inside the perturbed portion of the circuit are shown in blue. Network perturbation in the three cases consisted in demyelinating 25% of the segments along the axons of model neurons, by removing 70% of the myelin lamellae. In each case, 280 trials were simulated for one network. These simulations show an increased drift and diffusion inside the perturbed zone, consistent with the increased drift and diffusion when perturbing the entire network (Figure 6B and Supplementary Figure 11). In particular, spatially heterogeneous demyelination in our network leads to a bias away from the affected zone and to increased trial-to-trial variability. Note that this is a model prediction, but we are not aware of empirical data showing heterogeneous demyelination with aging. Further, note that while our network model has a topological ring structure, neurons in PFC are not anatomically arranged depending on their preferred features. Thus, spatially heterogeneous demyelination would likely affect neurons with different feature preferences (i.e., neurons throughout our ring model).

(4) The bump attractor model of WM relies on a continuous attractor dynamics to encode the information stored in memory --a fixed point dynamics that can only vary via the slow noise-driven drift. This means, as the authors mention, that changes in CV won't affect the performance of WM in their model. This seems to be a limitation of the model, or at least an effect which is highly dependent on the modeler's choice, rather than an accurate prediction. While testing the effects of oscillations (as the authors argue in the Discussion) might be out of the scope of this work, there are other WM models which are more sensitive to temporal differences in activity. The authors should test whether the same (lack of) effects are also found in other WM models. A silent WM model seems to be the ideal candidate for this, as the authors already have the key dynamics of that model incorporated in their computational framework (namely, short-term synaptic facilitation in excitatory synapses).

We fully agree that considering the effects of demyelination in networks with alternative mechanisms would strengthen our manuscript. As suggested by the reviewer, we have simulated demyelination effects (AP failures and changes in CV) in an activity silent working memory model. The results are described in detail above in our response to the public review of the same reviewer.

We also would like to mention that we have now also tested larger conduction delays in the bump attractor model, revealing additional working memory errors. This is shown in the revised version of Supplementary Figure 6 (see below). However, those delays are unrealistically large and thus the main effect in both the bump attractor and the activity-silent model is due to AP failures.

Author response image 6.

Effect of propagation delays on control and perturbed networks. (A) Memory strength (left panels) and diffusion (right panels) for the young, control networks with zero propagation delays (blue solid line), as in Figure 5, and with propagation delays from a uniform distribution with a range between 0 and 100 ms (yellow dashed line). (B) Memory strength and diffusion for perturbed networks when demyelinating 50% of the segments along the axons of model neurons, by removing 60% of the myelin lamellae without delays (red solid line), and with delays from a uniform distribution with a range between 0 and 40 ms (gray dashed line) and between 0 and 85 ms (black dash-dotted line). The measures of working memory performance were calculated by averaging across 20 networks and 280 trials for each network. Shaded areas indicate SEM for each case. For the young, control networks, there was no difference with and without propagation delays, even though the delays used in the network simulations were much larger than the delays quantified in the single neuron model (the longest delays found for the most extreme perturbation condition –demyelination of 75% of the segments by removing 100% of the myelin lamellae– were of 49.9 ms on average; A). Working memory performance was also unaffected in the perturbed network with AP failures for delays ranging between 0 and 40 ms, also larger than the ones quantified in the single neuron model (for the case of 50% of the segments demyelinated by removing 60% of the myelin lamellae, the average delay in the cohort was 4.6 ms and the maximum delay was 15.7 ms; B). However, including extremely long delays of up to 85 ms did further impair memory compared to the impairment level introduced by AP failures alone (B).

(5) Impact of demyelination and remyelination on working memory: Could the authors explain here how these biologically detailed alterations are implemented in the bump attractor model? Is the CV and AP failure rate adjusted to the values produced by the multicompartment neuron model with these myelin alterations?

Yes, the reviewer is right, the CV and AP failure rate have been adjusted to the values produced by the multicompartment neuron model. To clarify this in the manuscript, we have restated the text as follows:

Lines 243 - 249 (Results):

To investigate how myelin alterations affect working memory maintenance, we explored in the network model the same demyelination and remyelination conditions as we did in the single neuron model. Because our network model consists of point neurons (i.e., without detailed axons), we incorporated CV slowing as an effective increase in synaptic transmission delays (see Methods). To simulate AP failures, we adjusted the AP failure rate to the values given by the single neuron model, by creating a probabilistic model of spike transmission from the excitatory presynaptic neurons to both the excitatory and inhibitory postsynaptic neurons (see Methods).

Lines 722 - 747 (Methods):

Modeling action potential propagation failures in the network. The network model is composed of point neurons without an explicit model of the axon. To effectively model the action potential failures at the distal end of the axons quantified with the single neuron model under the different demyelination and remyelination conditions, the AP failure rate was adjusted to the values produced by the single neuron model. To do this, we perturbed the 10 control networks by designing a probabilistic model of spike transmission from the excitatory presynaptic neurons to both the excitatory and inhibitory postsynaptic neurons. From the single neuron model, for each demyelination/remyelination condition, we quantified the probability of AP failure for each of the neurons in the control cohort, as well as the percentage of those neurons that shared the same probabilities of failure. That is, the percentage of neurons that had probability of failure = 0, probability of failure = 1 or any other probability. Then, we computed the probability of transmission, , and we specified for the corresponding percentages of excitatory neurons in the networks. Thus, in the network model, we took into account the heterogeneity observed in the single neuron model under each demyelination/remyelination condition.

Modeling conduction velocity slowing in the network. To explore the effect of CV slowing along the axons of model neurons, we simulated 20 young, control networks and 20 perturbed networks with AP failure rates adjusted for the case of single model neurons with 50% of the segments demyelinated along the axons by removing 60% of the myelin lamellae (we ran 280 trials for each network). Then, we added random delays uniformly distributed with a minimum value of 0 ms in both cases, a maximum value of 100 ms in the control networks, and a maximum values of 40 ms and 85 ms in the perturbed networks, in both the AMPA and NMDA excitatory connections to both E and I neurons (Supplementary Figure 6). These large values were chosen because we wanted to illustrate the potential effect of CV slowing in our network and smaller, more realistic, values did not have any effect.

(6) "We also sought to reveal the effect on working memory performance of more biologically realistic network models with AP transmission probabilities matched to both axons with intact and with altered myelin sheaths, as likely occurs in the aging brain (Figure 1). Thus, we ran network model simulations combining AP failure probabilities corresponding to groups of neurons containing intact axons and axons presenting different degrees of demyelination." I fail to see the difference with respect to the results in previous sections. Is it that now we have subnetworks in which axons are intact and subnetworks with significant AP failures, while before there was no topological separation between both cases? Please clarify.

In Figures 5 and 6 the AP failure rate of the neural population in the network simulations was matched to the AP failure rate of the cohort of single model neurons for each demyelination/remyelination condition. Since not all model neurons have equal features, a given condition produces different levels of impairment in its neuron. Thus, we quantified the probability of AP failure for each neuron in the control cohort, as well as the percentage of those neurons that shared the same probabilities of failure. Then, we computed the probability of AP transmission for the corresponding percentages of excitatory neurons in the networks. Thus, in the network model, we took into account the heterogeneity observed in the single neuron model under each demyelination/remyelination condition.

However, In Figures 7 and 8, we consider additional heterogeneity due to a different degree of demylination/remyelination of different neurons. Here, excitatory neurons in the network model are not perturbed according to a single demyelination/remyelination condition. Instead, we allowed that different percentages of excitatory neurons had AP failure rates corresponding to different demyelination/remyelination conditions: some were unperturbed, while others had different degrees of demyelination (Figure 7) and different degrees of remyelination (Figure 8). We have modified the text for clarification in several places.

First, when we describe the impact of demyelination on working memory, we already mention that (line 271): “In each of the 10 networks, we set the AP failure rate of the excitatory neurons according to the distribution of failure probabilities of the neurons in the single neuron cohort for the given demyelination or remyelination condition. Thus, we took into account the heterogeneity of demyelination and remyelination effects from our single neuron cohort (Figure 3A; Supplementary Figure 3). Note that this heterogeneity originates from differences in axon properties, but probabilities of failure for all neurons in the network correspond to the same degree of demyelination (Figure 6). We will also consider networks that contain different combinations of axons with either intact or perturbed myelin (Figure 7 and Figure 8).”

Second, we have combined the text describing Figures 7 and 8 under a single section title, which reads “Simulated heterogenous myelin alterations match empirical data” (line 334) and start this section with (line 337): “Up to this point we have studied network models with AP failure probabilities corresponding to a single degree of myelin alterations (i.e., with all excitatory neurons in the network having AP failure rates matched to those of the single neuron cohort for one particular demyelination or remyelination condition). Next, we sought to reveal the effect on working memory performance of more biologically realistic network models, where excitatory neurons in the networks were perturbed according to a combination of different demyelination or remyelination conditions. That is, we simulated networks with excitatory neurons having AP failure probabilities matched to both neuronal axons with intact and with altered myelin sheaths in different degrees, as likely occurs in the aging brain (Figure 1).”

(7) "Unexpectedly, our model indicates that compared to the performance of networks composed of neurons possessing axons with intact myelin sheaths, both demyelination and remyelination leads to an impaired performance." This conclusion is quite interesting, but I lack intuition from the paper as of why it is happening. In fact, the authors say in the Discussion that "complete remyelination of all the previously demyelinated segments with sufficient myelin, with fewer transitions between long and short segments, recovered working memory function." Would we then see a minimum and then an increase in memory duration in Figure 9B if we extended the X-axis until we hit 100% of new myelin sheaths?

This is a very important question that we have carefully addressed in Results and Discussion. We distinguish between two remyelination cases in the models. Complete remyelination: when all (100%) the previously demyelinated segments have been subsequently remyelinated, and incomplete remyelination: when less than 100% (25%, 50% or 75%) of the demyelinated segments have been remyelinated. Figure 6 (middle and right columns) shows the two cases (black lines for any percentage of lamellae added vs. colored lines): for 100% of the segments remyelinated, the network performance is nearly or completely (when enough lamellae are added) recovered to the young network performance. In fact, with the single neuron model we observe that (lines 192 - 193 in Results): “Remyelinating all affected segments with 75% of lamellae (the maximal amount of remyelination) nearly eliminated AP failures (1.8 ± 1.1%)”. However, incomplete remyelination recovers the performance compared to demyelination (middle and right columns in Figure 6 vs left column), but this performance is worse than the performance of the young networks. The single neuron model shows that (lines 194 - 197 in Results): “Incomplete remyelination, where some segments were still demyelinated, still had relatively high AP failure rates. For example, when one eighth of segments were remyelinated with the maximal amount of lamellae and one eighth were left bare, 25.7 ± 11.5% of APs failed across the cohort (Figure 4C, red dashed line and arrow).”

In Figure 9B (now Figure 8B), we combine intact axons with axons that are only partially remyelinated (i.e., incomplete remyelination). Extending the X-axis in Figure 8B until 100% of new myelin sheaths would not imply a minimum and a subsequent increase, but a continuous impairment: the more axons we perturb (remyelinate) the higher is the impairment compared to the young cases where all the axons are intact.

The sentence "Unexpectedly, our model indicates that compared to the performance of networks composed of neurons possessing axons with intact myelin sheaths, both demyelination and remyelination leads to an impaired performance.", now reads as (lines 379 380 in Results): “Therefore, both demyelination and incomplete remyelination lead to impaired performance in our networks, compared to networks with intact myelin sheaths”. We have also rewritten the corresponding section in Discussion (lines 486 - 489) as follows: “Therefore, it is reasonable to assume that ineffective remyelination may lead to working memory impairment. In fact, complete remyelination of all previously demyelinated segments with sufficient myelin, with fewer transitions between long and short segments, led to full recovery of working memory function.”

(8) [minor] "Our recent network model found that age-related changes in firing rates and synapse numbers in individual neurons can lead to working memory impairment (Ibañez et al., 2020), but did not consider myelin dystrophy." Could you be more precise about which age-related changes were studied in Ibanez et al. 2020? From the paper it seems like it was mostly cellular excitability and synaptic density, so this should be added here for more context.

To clarify this, we have added the following sentences in the Introduccion (line 105):

“Our recent network model revealed that the empirically observed age-related increase in AP firing rates in prefrontal pyramidal neurons (modeled through an increased slope of the f-I curve) and loss of up to 30% of both excitatory and inhibitory synapses (modeled as a decrease in connectivity strength) can lead to working memory impairment (Ibañez et al., 2020), but this model did not incorporate the known changes to myelin structure that occur during normal

aging.”

(9) [minor] "Recurrent excitatory synapses are facilitating, which promotes robust and reliable persistent activity despite spatial heterogeneities in the connectivity or in the intrinsic properties of the neurons." It would be great to add a reference here to justify the inclusion of this type of plasticity in the excitatory circuit (for example Wang, Markram et al. Nat Neuro 2006).

We have added the references suggested by the reviewer and a further one in the Results (line 216):

“Recurrent excitatory synapses are facilitating, as has been empirically observed in PFC (Hempel et al., 2000; Wang et al., 2006), which promotes robust and reliable persistent activity despite spatial heterogeneities in the connectivity or in the intrinsic properties of the neurons.”

References:

Hempel, C. M., Hartman, K. H., Wang, X. J., Turrigiano, G. G., and Nelson, S. B. (2000). Multiple forms of short-term plasticity at excitatory synapses in rat medial prefrontal cortex. J. Neurophysiol. 83, 3031–3041. doi: 10.1152/jn.2000.83.5.3031

Wang, Y., Markram, H., Goodman, P. H., Berger, T. K., Ma, J., and Goldman- Rakic, P. S.(2006). Heterogeneity in the pyramidal network of the medial prefrontal cortex. Nat.Neurosci. 9, 534–542. doi: 10.1038/nn1670

Author response:

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

Reviewers’ Comments:

Reviewer #1 (Remarks to the Author):

Summary:

Fang Huang et al found that RBM7 deficiency promotes metastasis by coordinating MFGE8 splicing switch and NF-kB pathway in breast cancer by utilizing clinical samples as well as cell and tail vein injection models.

Strengths:

This study uncovers a previously uncharacterized role of MFGE8 splicing alteration in breast cancer metastasis, and provides evidence supporting RBM7 function in splicing regulation. These findings facilitate the mechanistic understanding of how splicing dysregulation contributes to metastasis in cancer, a direction that has increasingly drawn attention recently, and provides a potentially new prognostic and therapeutic target for breast cancer.

We thank the reviewer for appreciating the novelty and importance of this study, and have provided new data to address the following concerns raised by the reviewer.

Weaknesses:

This study can be strengthened in several aspects by additional experiments or at least by further discussions. First, how RBM7 regulates NF-kB, and how it coordinates splicing and canonical function as a component of NEXT complex should be clarified. Second, although the roles of MFGE8 splicing isoforms in cell migration and invasion have been demonstrated in transwell and wound healing assays, it would be more convincing to explore their roles in vivo such as the tail vein injection model. Third, the clinical significance would be considerably improved, if the therapeutic value of targeting MFGE8 splicing could be demonstrated.

We’re thankful for the constructive suggestions. A preliminary study on the mechanism by which RBM7 regulates NF-kB pathway is already underway. We found RBM7 depletion remarkably promoted the expression of IL-1β as judged by qPCR and ELISA assays (new Figure S5G- S5I, also see below). IL-1β, commonly known as a pro-inflammatory cytokine, could bind to IL-1R and initiate a multistage enzymatic reaction that triggers the activation of NF-κB pathway (Axel Weber, 2010) (Qing Guo, 2024). Thus we speculated that the upregulation of IL-1β might be a causal factor in RBM7-depletion-induced activation of NF-kB signaling. It will be interesting to determine the complete molecular mechanism in our future study. In addition, we performed a co-IP experiment and found that RBM7 could interact with RNA splicing factor SF3B2, a component of spliceosomal U2 snRNP complex (new Figure S6B, also see below). Consistent with the AS regulation of MFGE8 by RBM7, the depletion of SF3B2 also promoted exon7 skipping, implying a cooperative effect of the two proteins in regulating MFGE8 splicing (new Figure S6C-6D, also see below). This is in concert with a previous study that RRM domain of RBM7 could bind a proline-rich segment within SF3B2 (Falk, Finogenova et al., 2016). The interaction mode with strong similarity to RBM7RRM–ZCCHC8Proline interaction in the NEXT complex indicated mutually exclusive binding of SF3B2 and ZCCHC8 to RBM7. Thus, RBM7 appears to play dual, but not conflicting, roles during RNA processes depending on its interaction with the spliceosome or exosome (see line 427-437 in the new manuscript).

Author response image 1.

The mRNA levels of IL-1β in MDA-MB-231 or BT549 cells with stable RBM7 knockdown or control vector were examined by qRT-PCR approach.

Author response image 2.

Supernatants from RBM7-knockdown MDA-MB-231 or BT549 cells were collected and protein expression of IL-1β was measured by ELISA kit.

Author response image 3.

The knockdown efficiency of RBM7 in two breast cancer cell lines were determined by qRT-PCR approach.

Author response image 4.

Immunoprecipitation assay was performed in breast cancer cells expressing HA-RBM7 and Flag-SF3B2 or empty vector. The Flag-tagged precipitated complexes and lysates were analyzed through western blotting.

Author response image 5.

The splicing shift of MFGE8 upon SF3B2 knockdown in breast cancer cells was examined by RT-PCR approach. The mean ± SD of PSI values derived from three independent replicates is shown.

Author response image 6.

The SF3B2 knockdown efficiency was examined by qRT-PCR.

To further corroborate the roles of two MFGE8 isoforms in cell invasion, we have performed Fluorescent Gelatin Degradation Assays for investigating invadopodia formation. Consistent with the transwell assay results, MFGE8-L up-regulation suppressed breast cancer cells invasion through a layer of extracellular matrix, whereas breast cancer cells with ectopic expression of MFGE8-S acquired enhanced ability to degrade matrix and invasion (new Figure 5B, also see below). In addition, to determine the therapeutic value of targeting MFGE8 splicing, we transfected triple-negative breast cancer cells with ASOs targeting RBM7-binding motif and examined the potential impact on cell aggressiveness. The results showed an obvious increase in exon7-skipped variant of MFGE8 as compared to the scramble negative control ASOs, meanwhile, the migrative and invasive ability of breast cancer cells treated with splice-targeting ASOs was significantly boosted (new Figure 6B and S5B, also see below), further suggesting that RBM7-knockdown stimulated aggressiveness of breast cancer at least partially relies on splicing switch of MFGE8.

Author response image 7.

Gelatin degradation assay was performed to test the effect of RBM7 knockdown on invadopodia function. 10000 cells were plated onto FITC-gelatin substrates (Green) and cultured for 48 h. Representative images are shown (red, Cy3-phalloidin; blue, DAPI) and the degraded areas were quantified by Image J software. Scar bars= 50 μm. P values were determined by one-way ANOVA with Tukey's multiple comparison test (n = 3).

Author response image 8.

Representative transwell analysis of migrative/invasive capability of breast cancer cells transfected with 500 nM ASO directed against RBM7-binding region in MFGE8 pre-mRNA. P values were determined by one-way ANOVA with Tukey's multiple comparison test.

Author response image 9.

RT-PCR quantification of two MFGE8 isoforms after transfecting breast cancer cells with 500 nM ASO directed against RBM7-binding region in MFGE8 pre-mRNA. P values were calculated by one-way ANOVA with Tukey's multiple comparison test.

The minor concerns

(1) Several figure legends do not match with the images, for example, Figure 2K, Figure 4, Figure 7D, and 7E, and the description of Fiure 7F is missing in the text.

As suggested by the reviewer, we have checked all of the figure legends carefully and corrected all of the misinterpretation.

(2) The statistical methods for Figure1A and Figure1B should be indicated.

As suggested by the reviewer, we have included the statistical methods for Figure1A and 1B in Figure1 legend. Data in Figure 1A and 1B are presented as means ± SD and P values were obtained by Mantel-Cox log-rank test.

(3) The molecular weight of the proteins in the Western Blot images should be marked.

As suggested by the reviewer, we have added the molecular weight of proteins in all of the western blot images.

(4) The sequences where RBM7 binds on MFGE8 RNA should be clearly indicated.

We thank the reviewer for this question. We analyzed the sequence of alternative exon 7 and the motifs nearby its 5’ or 3’ splice sites, and found two RBM7 potentially binding motifs are positioned in proximal to the pseudo 3’ splice site. Subsequent RT-PCR for the precipitation in RIP assays confirmed RBM7 could bind to the upstream sequence containing 5’-UUUCUU-3’ motifs adjacent to intron6/exon7 junction of MFGE8 cassette exon, but not another region nearby it. To pinpoint the location for the potential cis-element for AS regulation by RBM7, we designed antisense oligonucleotides (ASOs) to block RBM7 potentially binding sites (UUUCUU). As shown in revised Figure 4F, when compared to scramble ASO, targeting ASOs contributed to the exclusion of exon7. Additionally, we constructed an exogenous MFGE8 splicing reporter containing exon 6-8 and partial intron sequences to determine the binding site for AS regulation by RBM7. The depletion of RBM7 still induced the splicing shift of the minigene reporter by elevating MFGE8-S variant. While the binding motif UUUCUU was removed or mutated, RBM7 failed to affect the splicing outcomes of MFGE8 (new Figure S3C, also see below). Due to its close proximity to 3’ splice site, UUUCUU residues bound by RBM7 is very likely to participate in spliceosome assembly at the upstream 3’ splice site of exon7, which may explain why disruption of the motif led to almost complete exon7 skipping. The above data suggested that RBM7 regulated the exon skipping of MFGE8 by binding to UUUCUU located six nucleotides upstream of the 3’ splice-site of exon7.

Author response image 10.

Upper: the red line in diagram indicates ASOs targeting region which contains UUUCUU; down: MCF7 and MDA-MB-231 cells were transfected with ASOs targeting MFGE8 pre-mRNA for 48h and then applied for RT-PCR identification. P values were determined by one-way ANOVA with Tukey's multiple comparison test.

Author response image 11.

Upper: MFGE8 min-splicing reporters with mutation in the RBM7 binding site or a non-specific binding were generated and shown in cartoon; down: RT-PCR assays were performed to identify the splicing outcomes of MFGE8 reporter while RBM7 was depleted in breast cancer cells.

(5) Some typos, graphic errors, and sentences are hard to understand and need to be corrected, such as lines 80-81, 249-250, line 221 "motfs", line 319 "RBM4". Please carefully proofread and revise the entire manuscript.

As suggested by the reviewer, we have corrected typos and graphic errors mentioned above. In addition, this manuscript was also extensively edited to improve grammar and sentence structure.

(6) Define the abbreviations when they first appear, such as MFGE8-L, RBM, etc.

We thank the reviewer for raising this point. We have defined the abbreviations when firstly presented in the manuscript.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors reported the biological role of RBM7 deficiency in promoting metastasis of breast cancer. They further used a combination of genomic and molecular biology approaches to discover a novel role of RBM7 in controlling alternative splicing of many genes in cell migration and invasion, which is responsible for the RBM7 activity in suppressing metastasis. They conducted an in-depth mechanistic study on one of the main targets of RBM7, MFGE8, and established a regulatory pathway between RBM7, MFGE8-L/MFGE8-S splicing switch, and NF-κB signaling cascade. This link between RBM7 and cancer pathology was further supported by analysis of clinical data.

Strengths:

Overall, this is a very comprehensive study with lots of data, and the evidence is consistent and convincing. Their main conclusion was supported by many lines of evidence, and the results in animal models are pretty impressive.

Weaknesses:

However, there are some controls missing, and the data presentation needs to be improved. The writing of the manuscript needs some grammatical improvements because some of the wording might be confusing.

We thank the reviewer for the positive comments on this work, and have addressed all the concerns raised by the reviewer.

Specific comments:

(1) Figure 2. The figure legend is missing for Figure 2C, which caused many mislabels in the rest of the panels. The labels in the main text are correct, but the authors should check the figure legend more carefully. Also in Figure 2C, it is not clear why the authors choose to examine the expression of this subset of genes. The authors only refer to them as "a series of metastasis-related genes", but it is not clear what criteria they used to select these genes for expression analysis.

We thank the reviewer for raising this question. We have included the figure legend for Figure 2C and improved other figure legends throughout the article. For the second question, since gene ontology analysis of RNA-seq data in RBM7-depleted breast cancer cells showed that a series of differentially expressed genes were enriched in metastasis-associated processe, we identified the expression of this subset of genes in breast cancer cells in the presence or absence of RBM7 by heatmap differential analysis based on qRT-PCR results. To clarify this point and address the reviewer’s concern, we have improved the relevant description of this part (see line 174-180 in the new manuscript).

(2) Line 218-220. The comparison of PSI changes in different types of AS events is misleading. Because these AS events are regulated in different mechanisms, they cannot draw the conclusion that "the presence of RBM7 may promote the usage of alternative splice sites". For example, the regulators of SE and IR may even be opposite, and thus they should discuss this in different contexts. If they want to conclude this point, they should specifically discuss the SE and A5SS rather than draw an overall conclusion.

We are thankful for the reviewer’s valuable comment. According to the suggestion, we have removed the overall conclusion and corrected to discuss in SE and A5SS.

(3) In the section starting at line 243, they first referred to the gene and isoforms as "EFG-E8" or "EFG-E8-L", but later used "EFGE8" and "EFGE8-L". Please be consistent here. In addition, it will be more informative if the authors add a diagram of the difference between two EFGE8 isoforms in terms of protein structure or domain configuration.

As suggested by the reviewer, we keep using the name “MFGE8-L” for the canonical MFGE8 isoform and “MFGE8-S” for the truncated isoform in this manuscript. In addition, to clarify the structural basis for the different tumor invasion-related functions of two MFGE8 isoforms, we have included a diagram of their domain configuration in new Figure S4F and predicted protein structure in new Figure S4G. The details in the revised manuscript are given below:

Author response image 12.

Schematic diagram of the domain composition of two MFGE8 isoforms. Upper: the full-length variant with exon7 indicated by yellow square; down: the truncated variant with exon7 skipping.

Author response image 13.

The model structure of two MFGE8 isoforms was implemented using SwissModel software. The F5/8 type C2 protein domain excluded from MFGE8-S variant was marked in red.

(4) Figure 7B and 7C. The figures need quantification of the inclusion of MFGE exon7 (PSI value) in addition to the RT-PCR gel. The difference seems to be small for some patients.

As suggested by the reviewer, we have included the relative quantification of PSI for endogenous MFGE8 in breast cancer patients and found increased proportion of exon7 exclusion in most tumor samples when compared to normal tissues (case#1: 86:94; case#2: 84:86; case#3: 79:85; case#4: 63:75; case#5: 69:93; case#6: 71:80) (new Figure 7B, also see below). On the other hand, we have expanded the number of metastatic breast cancer cases and quantified the the AS events within MFGE8 by analyzing the PSI values. The lymph node metastases contain a higher proportion of MFGE8 variant with skipped exon7 in comparison with paired primary tumor tissues (case#1: 80:95; case#2: 86:97; case#3: 84:90; case#4: 70:78; case#5: 83:89) (Figure 7C). This is coherent with decreased RBM7 expression levels found in breast cancer with lymph node metastasis.

Author response image 14.

The splicing alteration of MFGE8 in 6 pairs of primary breast cancer tissues and adjacent normal tissues was examined using RT-PCR. The quantification of PSI vales was based on relative band intensities using Image J software.

Author response image 15.

The splicing alteration of MFGE8 in primary breast cancer tissues and corresponding lymph node metastases was identified by RT-PCR assays. The quantification of PSI vales wa determined by Image J software.

Minor comments:

The writing in many places is a little odd or somewhat confusing, I am listing some examples, but the authors need to polish the whole manuscript more to improve the writing. 1. Line 169-170, "...followed by profiling high-throughput transcriptome by RNA sequencing", should be "followed by high-throughput transcriptome profiling with RNA sequencing". 2. Line 170, "displayed a wide of RBM7-regulated genes were enriched...", they should add a "that" after the "displayed" as the sentence is very long. 3. Line 213, "PSI (percent splicing inclusion)" is not correct, PSI stands for "percent spliced in". 4. Line 216-217, the sentence is long and fragmented, they should break it into two sentences. 5. Line 224, the "tethering" should be changed to "recognizing". There is a subtle difference in the mechanistic implication between these two words. 6. Line 250, should be changed to "...in the ratio of two MFGE8 isoforms".

We thank the detailed comments from the reviewer. The points mentioned above has been addressed one by one and this manuscript was also extensively edited to improve grammar and sentence structure for better understanding.

References

Axel Weber PW, Michael Kracht* (2010) Interleukin-1 (IL-1) Pathway. SCIENCESIGNALING.

Qing Guo1, Yizi Jin1,2, Xinyu Chen3, Xiaomin Ye4, Xin Shen5, Mingxi Lin1,2, Cheng Zeng1,2, Teng Zhou1,2 and Jian Zhang1,2 (2024) NF-κB in biology and targeted therapy: new insights and translational implications. Signal Transduction and Targeted Therapy.

Falk S, Finogenova K, Melko M, Benda C, Lykke-Andersen S, Jensen TH, Conti E (2016) Structure of the RBM7–ZCCHC8 core of the NEXT complex reveals connections to splicing factors. Nature Communications.

Author response:

eLife assessment

This useful study shows how genetic variation is associated with fecundity following a period of reproductive diapause in female Drosophila. The work identifies the olfactory system as central to successful diapause with associated changes in longevity and fecundity. While the genetic screening and methods used are solid, the approach to assessing diapause is incomplete and could benefit from additional orthogonal experiments.

Response: We agree that, as with most studies, additional follow-up work will be informative.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The paper begins with phenotyping the DGRP for post-diapause fecundity, which is used to map genes and variants associated with fecundity. There are overlaps with genes mapped in other studies and also functional enrichment of pathways including most surprisingly neuronal pathways. This somewhat explains the strong overlap with traits such as olfactory behaviors and circadian rhythm. The authors then go on to test genes by knocking them down effectively at 10 degrees. Two genes, Dip-gamma and sbb, are identified as significantly associated with post-diapause fecundity, and they also find the effects to be specific to neurons. They further show that the neurons in the antenna but not the arista are required for the effects of Dip-gamma and sbb. They show that removing the antenna has a diapause-specific lifespan-extending effect, which is quite interesting. Finally, ionotropic receptor neurons are shown to be required for the diapause-associated effects.

Strengths and Weaknesses:

Overall I find the experiments rigorously done and interpretations sound. I have no further suggestions except an ANOVA to estimate the heritability of the post-diapause fecundity trait, which is routinely done in the DGRP and offers a global parameter regarding how reliable phenotyping is. A minor point is I cannot find how many DGRP lines are used.

Response: Thank you for the suggestions. We screened 193 lines and we will add that information to the methods.

Additionally, we will add the heritability estimate of the post-diapause fecundity trait.

Reviewer #2 (Public Review):

Summary

In this study, Easwaran and Montell investigated the molecular, cellular, and genetic basis of adult reproductive diapause in Drosophila using the Drosophila Genetic Reference Panel (DGRP). Their GWAS revealed genes associated with variation in post-diapause fecundity across the DGRP and performed RNAi screens on these candidate genes. They also analyzed the functional implications of these genes, highlighting the role of genes involved in neural and germline development. In addition, in conjunction with other GWAS results, they noted the importance of the olfactory system within the nervous system, which was supported by genetic experiments. Overall, their solid research uncovered new aspects of adult diapause regulation and provided a useful reference for future studies in this field.

Strengths:

The authors used whole-genome sequenced DGRP to identify genes and regulatory mechanisms involved in adult diapause. The first Drosophila GWAS of diapause successfully uncovered many QTL underlying post-diapause fecundity variations across DGRP lines. Gene network analysis and comparative GWAS led them to reveal a key role for the olfactory system in diapause lifespan extension and post-diapause fecundity.

Weaknesses:

(1) I suspect that there may be variation in survivorship after long-term exposure to cold conditions (10ºC, 35 days), which could also be quantified and mapped using genome-wide association studies (GWAS). Since blocking Ir21a neuronal transmission prevented flies from exiting diapause, it is possible that natural genetic variation could have a similar effect, influencing the success rate of exiting diapause and post-diapause mortality. If there is variation in this trait, could it affect post-diapause fecundity? I am concerned that this could be a confounding factor in the analysis of post-diapause fecundity. However, I also believe that understanding phenotypic variation in this trait itself could be significant in regulating adult diapause.

Response: We agree that it is possible that the ability to endure cool temperatures per se may influence post-diapause fecundity. However, cool temperature is the essential diapause-inducing condition in Drosophila, so it is not obvious how to separate those effects experimentally, and we agree that phenotypic variation in the cool-sensitivity trait itself could be significant in regulating diapause.

(2) On p.10, the authors conclude that "Dip-𝛾 and sbb are required in neurons for successful diapause, consistent with the enrichment of this gene class in the diapause GWAS." While I acknowledge that the results support their neuronal functions, I remain unconvinced that these genes are required for "successful diapause". According to the RNAi scheme (Figure 4I), Dip-γ and sbb are downregulated only during the post-diapause period, but still show a significant effect, comparable to that seen in the nSyb Gal4 RNAi lines (Figure 4K).

Response: Our definition of successful diapause is the ability to produce viable adult progeny post-diapause, which requires that the flies enter, maintain, and exit diapause, alive and fertile. We will restate our conclusion to say that Dip-γ and sbb are required for post-diapause fecundity.

In addition, two other RNAi lines (SH330386, 80461) that did not show lethality did not affect post-diapause fecundity.

Response: We interpret those results to mean that those RNAi lines were not effective since Dip-γ and sbb are known to be essential.

Notably, RNAi (27049, KK104056) substantially reduced non-diapause fecundity, suggesting impairment of these genes affects fecundity in general regardless of diapause experience. Therefore, the reduced post-diapause fecundity observed may be a result of this broader effect on fecundity, particularly in a more "sensitized" state during the post-diapause period, rather than a direct regulation of adult diapause by these genes.

Response: Ubiquitous expression of RNAi lines #27049 or #KK104056 was lethal, so we included the tubGAL80ts repressor to prevent RNAi from taking effect during development. Flies had to be shifted to 30 °C to inactivate the repressor and thereby activate the RNAi. At 30 °C, fecundity of the controls (GFP RNAi lines #9331, KK60102) were also lower (average non-diapause fecundity = 12 and 19 respectively) and similar to #27049 or #KK104056. We also assessed the knockdown using Repo GAL4 and nSyb GAL4 and did not find a significant difference/decline in the non diapause fecundity for #27049 and #KK104056 as compared to a nonspecific RNAi control (#54037).

(3) The authors characterized 546 genetic variants and 291 genes associated with phenotypic variation across DGRP lines but did not prioritize them by significance. They did prioritize candidate genes with multiple associated variants (p.9 "Genes with multiple SNPs are good candidates for influencing diapause traits."), but this is not a valid argument, likely due to a misunderstanding of LD among variants in the same gene. A gene with one highly significantly associated variant may be more likely to be the causal gene in a QTL than a gene with many weakly associated variants in LD. I recommend taking significance into account in the analysis.

We agree with the reviewer, and in Supplemental Table S3 we list top-associated SNPs in order from the lowest (most significant) p-value. Most of the top-associated genes from this analysis were uncharacterized CG numbers for which there were insufficient tools available for validation purposes. Nevertheless, there is overlap amongst the highly significant genes by p-value and those with multiple SNPs. Amongst the top 15 genes with multiple associated SNPsCG18636 & CR15280 ranked 3rd by p-value, CG7759 ranked 4th, CG42732 ranked 10th, and Drip ranked 30th (all above the conservative Bonferroni threshold of 4.8e-8) while three Sbb-associated SNPs also appear in Table 3 above the standard e-5 threshold.

Reviewer #3 (Public Review):

Summary:

Drosophila melanogaster of North America overwinters in a state of reproductive diapause. The authors aimed to measure 'successful' D. melanogaster reproductive diapause and reveal loci that impact this quantitative trait. In practice, the authors quantified the number of eggs produced by a female after she exited 35 days of diapause. The authors claim that genes involved with olfaction in part contribute to some of the variation in this trait.

Strengths:

The work used the power platform of the fly DRGP/GWAS. The work tried to verify some of the candidate loci with targeted gene manipulations.

Weaknesses:

Some context is needed. Previous work from 2001 established that D. melanogaster reproductive diapause in the laboratory suspends adult aging but reduces post-diapause fecundity. The work from 2001 showed the extent fecundity is reduced is proportional to diapause duration. As well, the 2001 data showed short diapause periods used in the current submission reduce fecundity only in the first days following diapause termination; after this time fecundity is greater in the post-diapause females than in the non-diapause controls.

Response: The 2001 paper by Tatar et al. reports the number of eggs laid after 3, 6, or 9 weeks in diapause conditions. Thus the diapause conditions used in this study (35 days or 5 weeks) are neither short nor long, rather intermediate. Does the reviewer have a specific concern?

In this context, the submission fails to offer a meaningful concept for what constitutes 'successful diapause'. There is no biological rationale or relationship to the known patterns of post-diapause fecundity. The phenotype is biologically ambiguous.

Response: We have unambiguously defined successful diapause as the ability to produce viable adult progeny post-diapause. Other groups have measured % of flies that arrest ovarian development or % of post-diapause flies with mature eggs in the ovary, or # eggs laid post-diapause; however we suggest that # of viable adult progeny produced post-diapause is more meaningful than the other measurements from the point of view of perpetuating the species.

I have a serious concern about the antenna-removal design. These flies were placed on cool/short days two weeks after surgery. Adults at this time will not enter diapause, which must be induced soon after eclosion. Two-week-old adults will respond to cool temperatures by 'slowing down', but they will continue to age on a time scale of day-degrees. This is why the control group shows age-dependent mortality, which would not be seen in truly diapaused adults. Loss of antennae increases the age-dependent mortality of these cold adults, but this result does not reflect an impact on diapause.

Response: The reviewer has a point. We carried out the lifespan study under two different conditions: either by removing the antenna and moving the flies directly to 10 °C or by removing the antenna and allowing a “wound healing” period prior to moving the flies to 10 °C (out of concern that the flies might have died quickly because wound healing may be impaired at 10 °C). In both cases, lifespan was shortened. We will add a discussion of the technical limitations of this experiment.

• Appraisal of whether the authors achieved their aims, and whether the results support their conclusions.

The work falls well short of its aim because the concept of 'successful diapause' is not biologically established. The paper studies post-diapause fecundity, and we don't know what that means. The loci identified in this analysis segregate for a minimally constructed phenotype. The results and conclusions are orthogonal.

Response: It is unclear to us why the reviewer has such a negative opinion of measuring post-diapause fecundity, specifically the ability to produce viable progeny post-diapause. The value of this measurement seems obvious from the point of view of perpetuating the species.

• The likely impact of the work on the field, and the utility of the methods and data to the community.

The work will have little likely impact. Its phenotype and operational methods are weakly developed. It lacks insight based on the primary literature on post-diapause. The community of insect diapause investigators are not likely to use the data or conclusions to understand beneficial or pest insects, or the impact of a changing climate on how they over-winter.

Response: The reviewer has not explained why his/her opinion is so negative.

Author response:

To Reviewer #1:

Thank you for your thorough review and comments on our work, which you described as “the role of neuritin in T cell biology studied here is new and interesting.”.  We have summarized your comments into two categories: biology and investigation approach, experimental rigor, and data presentation.

Biology and Investigation approach comments:

(1) Questions regarding the T cell anergy model:

Major point “(4) Figure 1E-H. The authors assume that this immunization protocol induces anergic cells, but they provide no experimental evidence for this. It would be useful to show that T cells are indeed anergic in this model, especially those that are OVA-specific. The lack of IL-2 production by Cltr cells could be explained by the presence of fewer OVA-specific cells, rather than by an anergic status.”

T cell anergy is a well-established concept first described by Schwartz’s group. It refers to the hyporesponsive T cell functional state in antigen-experienced CD4 T cells (Chappert and Schwartz, 2010; Fathman and Lineberry, 2007; Jenkins and Schwartz, 1987; Quill and Schwartz, 1987).  Anergic T cells are characterized by their inability to expand and to produce IL2 upon subsequent antigen re-challenge. In this paper, we have borrowed the existing in vivo T cell anergy induction model used by Mueller’s group for T cell anergy induction (Vanasek et al., 2006).  Specifically, Thy1.1+ Ctrl or Nrn1-/- TCR transgenic OTII cells were co-transferred with the congenically marked Thy1.2+ WT polyclonal Treg cells into TCR-/- mice.  After anergy induction, the congenically marked TCR transgenic T cells were recovered by sorting based on Thy1.1+ congenic marker, and subsequently re-stimulation ex vivo with OVA323-339 peptide. We evaluated the T cell anergic state based on OTII cell expansion in vivo and IL2 production upon OVA323-339 restimulation ex vivo.  

“The authors assume that this immunization protocol induces anergic cells, but they provide no experimental evidence for this.”

Because the anergy model by Mueller's group is well established (Vanasek et al., 2006), we did not feel that additional effort was required to validate this model as the reviewer suggested. Moreover, the limited IL2 production among the control cells upon restimulation confirms the validity of this model.

“The lack of IL-2 production by Cltr cells could be explained by the presence of fewer OVAspecific cells, rather than by an anergic status”.

Cells from Ctrl and Nrn1-/- mice on a homogeneous TCR transgenic (OTII) background were used in these experiments. The possibility that substantial variability of TCR expression or different expression levels of the transgenic TCR could have impacted IL2 production rather than anergy induction is unlikely.

Overall, we used this in vivo anergy model to evaluate the Nrn1-/- T cell functional state in comparison to Ctrl cells under the anergy induction condition following the evaluation of Nrn1 expression, particularly in anergic T cells.  Through studies using this anergy model, we observed a significant change in Treg induction among OTII cells. We decided to pursue the role of Nrn1 in Treg cell development and function rather than the biology of T cell anergy as evidenced by subsequent experiments.

Minor points “(6) On which markers are anergic cells sorted for RNAseq analysis?”

Cells were sorted out based on their congenic marker marking Ctrl or Nrn1-/- OTII cells transferred into the host mice.  We did not specifically isolate anergic cells for sequencing.

(2) Question regarding the validity of iTreg differentiation model.

Major point: “(5) Figure 2A-C and Figure 3. The use of iTregs to try to understand what is happening in vivo is problematic. iTregs are cells that have probably no equivalent in vivo, and so may have no physiological relevance. In any case, they are different from pTreg cells generated in vivo. Working with pTreg may be challenging, that is why I would suggest generating data with purified nTreg. Moreover, it was shown in the article of Gonzalez-Figueroa 2021 that Nrn1-/- nTreg retained a normal suppressive function, which would not be what is concluded by the authors of this manuscript. Moreover, we do not even know what the % of Foxp3 cells is in the iTreg used (after differentiation and 20h of re-stimulation) and whether this % is the same between Ctlr and Nrn1 KO cells.”.

We thank Reviewer #1 for their feedback. While it is true that iTregs made in vitro and in vivo generated pTregs display several distinctions (e. g., differences in Foxp3 expression stability, for example), we strongly disagree with this statement by Revieweer#1 “The use of iTregs to try to understand what is happening in vivo is problematic. iTregs are cells that have probably no equivalent in vivo, and so may have no physiological relevance.” The induced Treg cell (iTreg) model was established over 20 years ago (Chen et al., 2003; Zheng et al., 2002), and the model is widely adopted with over 2000 citations. Further, it has been instrumental in understanding different aspects of regulatory T cell biology (Hurrell et al., 2022; John et al., 2022; Schmitt and Williams, 2013; Sugiura et al., 2022).   

Because we have observed reduced pTreg generation in vivo, we choose to use the in vitro iTreg model system to understand the mechanistic changes involved in Treg cell differentiation and function, specifically, neuritin’s role in this process. We have made no claim that iTreg cell biology is identical to pTreg generated in vivo or nTreg cells. However, the iTreg culture system has proved to be a good in vitro system for deciphering molecular events involved in complex processes. As such, it remains a commonly used approach by many research groups in the Treg cell field (Hurrell et al., 2022; John et al., 2022; Sugiura et al., 2022). Moreover, applying the iTreg in vitro culture system has been instrumental in helping us identify the cell electrical state change in Nrn1-/- CD4 cells and revealed the biological link between Nrn1 and the ionotropic AMPA receptor (AMPAR), which we will discuss in the subsequent discussion. It is technically challenging to use nTreg cells for T cell electrical state studies due to their heterogeneous nature from development in an in vivo environment and the effect of manipulation during the nTreg cell isolation process, which can both affect the T cell electrical state.   

“Moreover, it was shown in the article of Gonzalez-Figueroa 2021 that Nrn1-/- nTreg retained a normal suppressive function, which would not be what is concluded by the authors of this manuscript.” 

We have also carried out nTreg studies in vitro in addition to iTreg cells. Similar to Gonzalez-Figueroa et al.'s findings, we did not observe differences in suppression function between Nrn1-/- and WT nTreg using the in vitro suppression assay. However, Nrn1-/- nTreg cells revealed reduced suppression function in vivo (Fig. 2D-L). In fact, Gonzalez-Figueroa et al. observed reduced plasma cell formation after OVA immunization in Treg-specific Nrn1-/- mice, implicating reduced suppression from Nrn1-/- follicular regulatory T (Tfr) cells. Thus, our observation of the reduced suppression function of Nrn1-/- nTreg toward effector T cell expansion, as presented in Fig. 2D-L, does not contradict the results from Gonzalez-Figueroa et al. Rather, the conclusions of these two studies agree that Nrn1 can play important roles in immune suppression observable in vivo that are not captured readily by the in vitro suppression assay.

“Moreover, we do not even know what the % of Foxp3 cells is in the iTreg used (after differentiation and 20h of re-stimulation) and whether this % is the same between Ctlr and Nrn1 KO cells.”

We have stated in the manuscript on page 7 line 208 that “Similar proportions of Foxp3+ cells were observed in Nrn1-/- and Ctrl cells under the iTreg culture condition, suggesting that Nrn1 deficiency does not significantly impact Foxp3+ cell differentiation”. In the revised manuscript, we will include the data on the proportion of Foxp3+ cells before iTreg restimulation.

(3) Confirmation of transcriptomic data regarding amino acids or electrolytes transport change

Minor point“(3) Would not it be possible to perform experiments showing the ability of cells to transport amino acids or electrolytes across the plasma membrane? This would be a more interesting demonstration than transcriptomic data.”

We appreciate Review# 1’s suggestion regarding “perform experiments showing the ability of cells to transport amino acids or electrolytes across the plasma membrane”.  We have indeed already performed such experiments corroborating the transcriptomics data on differential amino acid and nutrient transporter expression. Specifically, we loaded either iTreg or Th0 cells with membrane potential (MP) dye and measured MP level change after adding the complete set of amino acids (complete AA).  Upon entry, the charge carried by AAs may transiently affect cell membrane potential. Different AA transporter expression patterns may show different MP change patterns upon AA entry, as we showed in Author response image 1. We observed reduced MP change in Nrn1-/- iTreg compared to the Ctrl, whereas in the context of Th0 cells, Nrn1-/- showed enhanced MP change than the Ctrl. We can certainly include these data in the revised manuscript.

Author response image 1.

Membrane potential change induced by amino acids entry. a. Nrn1-/- or WT iTreg cells loaded with MP dye and MP change was measured upon the addition of a complete set of AAs. b. Nrn1-/- or WT Th0 cells loaded with MP dye and MP change was measured upon the addition of a complete set of AAs.

(4) EAE experiment data assessment

Minor point ”(5) Figure 5F. How are cells re-stimulated? If polyclonal stimulation is used, the experiment is not interesting because the analysis is done with lymph node cells. This analysis should either be performed with cells from the CNS or with MOG restimulation with lymph node cells.”

In the EAE study, the Nrn1-/- mice exhibit similar disease onset but a protracted non-resolving disease phenotype compared to the WT control mice.  Several reasons may contribute to this phenotype: 1. Enhanced T effector cell infiltration/persistence in the central nervous system (CNS); 2. Reduced Treg cell-mediated suppression to the T effector cells in the CNS; 3. Protracted non-resolving inflammation at the immunization site has the potential to continue sending T effector cells into CNS, contributing to persistent inflammation. Based on this reasoning, we examined the infiltrating T effector cell number and Treg cell proportion in the CNS.  We also restimulated cells from draining lymph nodes close to the inflammation site, looking for evidence of persistent inflammation.  When mice were harvested around day 16 after immunization, the inflammation at the local draining lymph node should be at the contraction stage.  We stimulated cells with PMA and ionomycin intended to observe all potential T effector cells involved in the draining lymph node rather than only MOG antigen-specific cells.  We disagree with Reviewer #1’s assumption that “This analysis should either be performed with cells from the CNS or with MOG restimulation with lymph node cells.”. We think the experimental approach we have taken has been appropriately tailored to the biological questions we intended to answer.

Experimental rigor and data presentation.

(1) Data labeling and additional supporting data

Major points (2) The authors use Nrn1+/+ and Nrn1+/- cells indiscriminately as control cells on the basis of similar biology between Nrn1+/+ and Nrn1+/- cells at homeostasis. However, it is quite possible that the Nrn1+/- cells have a phenotype in situations of in vitro activation or in vivo inflammation (cancer, EAE). It would be important to discriminate Nrn1+/- and Nrn1+/+ cells in the data or to show that both cell types have the same phenotype in these conditions too.

(3) Figure 1A-D. Since the authors are using the Nrp1 KO mice, it would be important to confirm the specificity of the anti-Nrn1 mAb by FACS. Once verified, it would be important to add FACS results with this mAb in Figures 1A-C to have single-cell and quantitative data as well.

Minor points  

(1) Line 119, 120 of the text. It is said that one of the most up-regulated genes in anergic cells is Nrn1 but the data is not shown.

(2) For all figures showing %, the titles of the Y axes are written in an odd way. For example, it is written "Foxp3% CD4". It would be more conventional and clearer to write "% Foxp3+ / CD4+" or "% Foxp3+ among CD4+".

(4) For certain staining (Figure 3E, H) it would be important to show the raw data, in addition to MFI or % values.

We can adapt the labeling and provide additional data, including Nrn1 staining on Treg cells and flow graphs for pmTOR and pS6 staining (Fig. 3H), as requested by Reviewer #1.

(2) Experimental rigor:

General comments:

“However, it is disappointing that reading this manuscript leaves an impression of incomplete work done too quickly.”

We were discouraged to receive the comment, “this manuscript leaves an impression of incomplete work done too quickly.” Our study of this novel molecule began without any existing biological tools such as antibodies, knockout mice, etc.  Over the past several years, we have established our own antibodies for Nrn1 detection, obtained and characterized Nrn1 knockout mice, and utilized multiple approaches to identify the molecular mechanism of Nrn1 function. Through the use of the in vitro iTreg system described in this manuscript, we identified the association of Nrn1 deficiency with cell electrical state change, potentially connected to AMPAR function. We have further corroborated our findings by generating Nrn1 and AMPAR T cell specific double knockout mice and confirmed that T cell specific AMPAR deletion could abrogate the phenotype caused by the Nrn1 deficiency (see Author response image 2).  We did not include the double knockout data in the current manuscript because AMPAR function has not yet been studied thoroughly in T cell biology, and we feel this topic warrants examination in its own right.  However, the unpublished data support the finding that Nrn1 modulates the T cell electrical state and, consequently, metabolism, ultimately influencing tolerance and immunity.  In its current form, the manuscript represents the first characterization of the novel molecule Nrn1 in anergic cells, Tregs, and effector T cells. While this work has led to several exciting additional questions, we disagree that the novel characterization we have presented Is incomplete. We feel that our present data set, which squarely highlights Nrn1’s role as an important immune regulator while shedding unprecedented light on the molecular events involved, will be of considerable interest to a broad field of researchers.

“Multiple models have been used, but none has been studied thoroughly enough to provide really conclusive and unambiguous data. For example, 5 different models were used to study T cells in vivo. It would have been preferable to use fewer, but to go further in the study of mechanisms.”

We have indeed used multiple in vivo models to reveal Nrn1's function in Treg differentiation, Treg suppression function, T effector cell differentiation and function, and the overall impact on autoimmune disease. Because the impact of ion channel function is often context-dependent, we examined the biological outcome of Nrn1 deficiency in several in vivo contexts.  We would appreciate it if Reviewer#1 would provide a specific example, given the Nrn1 phenotype, of how to proceed deeper to investigate the electrical change in the in vivo models.

“Major points (1) A real weakness of this work is the fact that in most of the results shown, there are few biological replicates with differences that are often small between Ctrl and Nrn1 -/-. The systematic use of student's t-test may lead to thinking that the differences are significant, which is often misleading given the small number of samples, which makes it impossible to know whether the distributions are Gaussian and whether a parametric test can be used. RNAseq bulk data are based on biological duplicates, which is open to criticism.”

We respectfully disagree with Reviewer #1 on the question of statistical power and significance to our work. We have used 5-8 mice/group for each in vivo model and 3-4 technical replicates for the in vitro studies, with a minimum of 2-3 replicate experiments. These group sizes and replication numbers are in line with those seen in high-impact publications. While some differences between Ctrl and Nrn1-/- appear small, they have significant biological consequences, as evidenced by the various Nrn1-/- in vivo phenotypes. Furthermore, we believe we have subjected our data to the appropriate statistical tests to ensure rigorous analysis and representation of our findings.

To Reviewer #2.

We thank Reviewer #2 for the careful review of the manuscript. We especially appreciate the comments that “The characterizations of T cell Nrn1 expression both in vitro and in vivo are comprehensive and convincing. The in vivo functional studies of anergy development, Treg suppression, and EAE development are also well done to strengthen the notion that Nrn1 is an important regulator of CD4 responsiveness.”

“The major weakness of this study stems from a lack of a clear molecular mechanism involving Nrn1. “  

We fully understand this comment from Reviewer #2. The main mechanism we identified contributing to the functional defect of Nrn1-/- T cells involves novel effects on the electric and metabolic state of the cells. Although we referenced neuronal studies that indicate Nrn1 is the auxiliary protein for the ionotropic AMPA-type glutamate receptor (AMPAR) and may affect AMPAR function, we did not provide any evidence in this manuscript as the topic requires further in-depth study.   

For the benefit of this discussion, we include our preliminary Nrn1 and AMPAR double knockout data (Author response image 2), which indicates that abrogating AMPAR expression can compensate for the defect caused by Nrn1 deficiency in vitro and in vivo. This preliminary data supports the notion that Nrn1 modulates AMPAR function, which causes changes in T cell electric and metabolic state, influencing T cell differentiation and function.  

Author response image 2.

Deletion of AMPAR expression in T cells compensates for the defect caused by Nrn1 deficiency. Nrn1-/- mice were crossed with T cell-specific AMPAR knockout mice (AMPARfl/flCD4Cre+) mice. The following mice were generated and used in the experiment: T cell specific AMPAR-knockout and Nrn1 knockout mice (AKONKO), Nrn1 knockout mice (AWTNKO), Ctrl mice (AWTNWT). a. Deletion of AMPAR compensates for the iTreg cell defect observed in Nrn1-/- CD4 cells. iTreg live cell proportion, cell number, and Ki67 expression among Foxp3+ cells 3 days after aCD3 restimulation. b. Deletion of AMPAR in T cells abrogates the enhanced autoimmune response in Nrn1-/- Mouse in the EAE disease model. Mouse relative weight change and disease score progression after EAE disease induction.  

Ion channels can influence cell metabolism through multiple means (Vaeth and Feske, 2018; Wang et al., 2020). First, ion channels are involved in maintaining cell resting membrane potential. This electrical potential difference across the cell membrane is essential for various cellular processes, including metabolism (Abdul Kadir et al., 2018; Blackiston et al., 2009; Nagy et al., 2018; Yu et al., 2022). Second, ion channels facilitate the movement of ions across cell membranes. These ions are essential for various metabolic processes. For example, ions like calcium (Ca2+), potassium (K+), and sodium (Na+) play crucial roles in signaling pathways that regulate metabolism (Kahlfuss et al., 2020). Third, ion channel activity can influence cellular energy balance due to ATP consumption associated with ion transport to maintain ion balances (Erecińska and Dagani, 1990; Gerkau et al., 2019). This, in turn, can impact processes like ATP production, which is central to cellular metabolism. Thus, ion channel expression and function determine the cell’s bioelectric state and contribute to cell metabolism (Levin, 2021).

Because the AMPAR function has not been thoroughly studied using a genetic approach in T cells, we do not intend to include the double knockout data in this manuscript before fully characterizing the T cell-specific AMPAR knockout mice.  

“Although the biochemical and informatics studies are well-performed, it is my opinion that these results are inconclusive in part due to the absence of key "naive" control groups. This limits my ability to understand the significance of these data.

Specifically, studies of the electrical and metabolic state of Nrn1-/- inducible Treg cells (iTregs) would benefit from similar data collected from wild-type and Nrn1-/- naive CD4 T cells.”

We appreciate the reviewer’s comments. This comment reflects two concerns in data interpretation:

(1) Are Nrn1-/- naïve T cells fundamentally different from WT cells? Does this fundamental difference contribute to the observed electrical and metabolic phenotype in iTreg or Th0 cells? This is a very good question we will perform the experiments as the reviewer suggested. While Nrn1 is expressed at a basal (low) level in naïve T cells, deletion of Nrn1 may cause changes in naïve T cell phenotype.   

(2) Is the Nrn1-/- phenotype caused by Nrn1 functional deficiency or due to the secondary effect of Nrn1 deletion, such as non-physiological cell membrane structure changes?

We have done the following experiment to address this concern.  We have cultured WT T cells in the presence of Nrn1 antibody and compared the outcome with Nrn1-/- iTreg cells (Author response image 3). WT iTreg cells under antibody blockade exhibited similar changes as Nrn1-/- iTreg cells, confirming the physiological relevance of the Nrn1-/- phenotype.

Author response image 3.

Nrn1 antibody blockade in WT iTreg cell culture caused similar phenotypic change as in Nrn1-/- iTreg cells. Nrn1-/- and WT CD4 cells were differentiated under iTreg condition in the presence of anti-Nrn1 (aNrn1) antibody or isotype control for 3 days. Cells were restimulated with anti-CD3 and in the presence of aNrn1 or isotype. a. MP measured 18hr after anti-CD3 restimulation. b. live CD4 cell number and proportion of Ki67 expression among live cells three days after restimulation. c. The proportion of Foxp3+ cells among live cells three days after restimulation.  

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Author response:

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

We previously responded to reviewer comments in a previous iteration of this draft, edited the manuscript accordingly, and have no further comments on the majority of them. However, we performed additional analyses mainly in response to weaknesses Reviewer 1 highlighted related to “one shortcoming [being] the lack of a conceptual model explaining the results”, and the eLife assessment stating “the study falls short of providing a cogent interpretation of key findings, which could be of great interest and utility”. We provide a conceptual explanation that ties together many of our results, which we demonstrate using real data and further explore using simulated data – these analyses are in a new section titled “Increase in PGS effect for increasing percentiles of BMI itself, and its relation to R2 differences when stratifying by covariates”, with the Discussion also being updated accordingly.

Essentially, we demonstrate that the effect of PGSBMI increases as BMI itself increases (using quantile regression – newly created Figure 5). This finding helps explain the correlation between covariate main effects, interaction effects, and maximum R2 differences when stratifying on different covariates, and also why any one or combination of covariates did not seem to be of unusual interest. While this result readily explains why covariates with larger main effects have larger interaction effects, by itself it does not seem to explain the differences in R2 in covariate-stratified bins, but we show using portions of real data and simulated data that in the case of this study they are closely related.

Effectively, as the effect of PGSBMI increases, variance in the phenotype will also increase – so long as the residuals do not increase proportionately, this causes R2 to also increase as R2 directly depends on outcome variance. We demonstrate this using simulated data (newly created S Figure 2) and real data (newly created S Figure 3). So the largest R2 differences between certain covariate-stratified bins seems to be a direct consequence of those covariates also having the largest PGSBMI*covariate interaction effects. These results tie into our previous response to Reviewer 1, where essentially there is not only heteroskedasticity in the relationship between PGSBMI and BMI, but a cause of the heteroskedasticity is an increasing effect in PGSBMI as BMI itself increases.

In the Discussion, we highlight several broad implications of these findings. First, these results may, in part, provide a generalizable explanation for epistasis, as the effect of a PGS (or any individual SNP) seems to depend on phenotype, and as phenotype depends on many SNPs, the effect of PGS and individual SNPs depends on other SNPs. Second, these results may also provide a generalizable explanation for GxE, as, demonstrated in this paper, interaction effects for SNPs (or a PGS) may largely depend on the phenotypic value itself, rather than any specific environment(s) or combination of. Finally, related to our previous response to Reviewer 2, modeling effects of SNPs dependent on phenotype itself would almost certainly result in gains in PGS performance (and locus discovery), which should also be larger than e.g., just GxAge effects as we demonstrated in this manuscript.

Author response:

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

We thank the reviewers for their careful reading of our manuscript and their constructive comments. We have significantly improved the writing, consolidated figures, and include new experiments (see below). We now center the manuscript on the methods used and have updated the title to reflect this new emphasis. We have also added quantification with statistics, as described below. A detailed description of our improvements is provided below.

New data figures:   

• Fig 3 – fig supp 2 – new experiment with insulin-triggered endocytosis of InsR

• Fig 3 – fig supp 3 – new experiments, all using the same protein construct

• Fig 3 – movie–  new experiment with insulin-triggered endocytosis of InsR

• Fig 4 – added new vehicle-only negative control experiments

• Fig 5 – fig supp 1 – new negative control experiments with sequential exposures to 750 nm light

Added figure panels with quantification/statistics for:  Fig. 1F; , Figure 1- figure supp 2B, Figure 2B, D, Fig. 2 – fig supp 1B, D; Fig 2 – fig supp 2B;  Fig 2 – fig supp 3B;  

Reviewer #1:

(1) The paper might benefit from a more streamlined structure and a clearer emphasis on its findings. A possible way to enhance its impact might be to focus more on its methodological aspects. The methodological facets stand out as both innovative and impactful.

We thank the reviewer for this suggestion and have rewritten the manuscript to center the methods, with our applications to TRPV1 and the InsR serving as examples.

(2) Line 243: Please provide a reference for Tet3-Bu or clarify its origin in this study. A concise description would be helpful.

The Jang et al., 2020 and Jana et al., 2023 studies are cited and give the structure of Tet3-Bu in Figure 3A.

(3) Consider merging Figures 1 and 2 for clarity.  

Because the cell types and constructs expressed differ for the figures, we did not merge them. However, we moved Figure 1 to the supplement because it repeats previously published data.

(4) Lines 281 and 293 should refer to Figure 5C, not 5B.  

This is now corrected.

(5) Should the paper pivot towards methodology, combining Figures 6 and 7 might be more coherent. 

The experiments in Figures 6 and 7 are different, making it difficult to merge them. However, Figures 7 and 8 describe the same experimental approach applied to two different membrane proteins. To align with our new focus on the methods and deemphasis of the biological system, we have merged Figures 7 and 8.

(6) A brief discussion comparing the cell surface labeling techniques and the merits of the presented system would offer valuable context.

We agree that additional discussion here would be helpful but were also trying to satisfy Reviewer #3’s request to reduce review-like content that disrupts the flow of the primary results. We therefore did not add a discussion of cell-surface labeling techniques.

Reviewer #2:

(1) To monitor the phosphatidylinositol-3,4,5-trisphosphates, the pleckstrin homology (PH) domain from Akt was used. This PH domain is not specific for just PI(3,4,5)P3 as stated by the authors. The Akt PH domain also binds PI(3,4)P2. The observed PI3K localization increase will also increase PI(3,4)P2 concentrations so the observed responses may not be solely because of PI(3,4,5)P3…

…Repeating the PH domain experiments with a PH domain that is specific for just PI(3,4,5)P3, like GRP1 or Btk, would be useful to separate out any contributions from PI(3,4)P2.

We have repeated key experiments demonstrating optogenetic activation of PI3K with the Grp1-PH domain and included these data in Figure 1-figure supplement 2.

(2) The data in Figure 4 supplement was confusing to interpret since it is unclear whether a membrane protein with the Tet3 is being expressed at the same time as the ncAA for labeling or if the observed labeling is endogenous. If the observed labeling in Figure 4 supplement D is endogenous, then significant concerns come up regarding the background labeling of the sTCO-sulfo-Cy5 used in the rest of the experiments.

We have updated the data in this figure using the same protein (InsR-Tet3-Bu-GFP) for every sTCO-conjugated dye tested. The protein is also labelled with GFP, making it clear which cells in the field were transfected and which were not. The new panels showing the bright field images for each field further aid readers in identifying untransfected cells. We believe the new presentation addresses the reviewer’s concerns about distinguishing sTCO labeling of Tet3-Bu-incorporating protein from labeling of endogenous proteins.

(3) I recommend reorganizing the article to be more linear. For example, Figure 4 is not fully explained until after Figure 4 supplement and Figure 5. This non-linear organization required a lot of back and forth reading to fully understand the logic of the experiments as well as the conclusions. 

We have improved the presentation along the lines suggested by the reviewer.

(4) The InsR data is interesting as a proof of concept however the writing around the InsR looks like an afterthought. The explanation for why InsR is chosen, what is known and unknown about its trafficking is given secondary importance in the writing but not in the figures. This difference weakens the article.  

We have improved the presentation along the lines suggested by the reviewer.

(5) Line 244 should read Figure 4A.  

This is now corrected.

(6) Line 281 should read Figure 5C.  

This is now corrected.

(7) Line 645. Fig 4, says C and E were shown as inverted b&w images when they aren't.  

This is now corrected.

(8) Fig 8. Line 702. States that these are TRPV1 positive cells but the figure is about InsR.

This is now corrected.

Reviewer #3:

(1) The Results section is lengthy and disorganized. Consider revising it for better clarity and conciseness. For instance, moving lines 157 and 166-170 to the Discussion or Methods section can streamline the Results section.  

We have improved the presentation along the lines suggested by the reviewer.

(2) Provide more specificity in reporting: In lines 139-170, clarify why you chose to use PhyB and this particular technique. Eliminate extraneous details and maintain a more concise narrative.

We have improved the presentation along the lines suggested by the reviewer.

(3) Avoid excessive review-like content, and keep the Results section focused on presenting novel findings. Simplify lines 4 173-185 to provide a straightforward presentation of results rather than extensive references to previous work.

We have improved the presentation along the lines suggested by the reviewer.

(4) Reevaluate lines 196-204 to determine if they are best suited for the Results section or if they could be moved to the Discussion or Methods for improved focus.

We have improved the presentation along the lines suggested by the reviewer.

(5) 231-238, revise the content to be more concise and directly to the point.  

We have improved the presentation along the lines suggested by the reviewer.

(6) Limit the number of figures to a maximum of five and restructure them to enhance readability. Consider consolidating panels from Figures 1 (which replicates previouslypublished work), 2, and 3 into a single figure to improve organization and information flow. 

See response to Reviewer #1, Comment #3. Although we did not merge Figures 2 and 3, we have consolidated the writing to improve the flow of the writing.

(7) Move Fig 5, which depicts control experiments, to supplementary information to improve the overall flow of the paper. Also, Figure 5 comes in the text before Figure 4 C-F and before Figure 4- supp1, so placing it in supplementary information would fix this issue. 

We have moved this figure to the supplement as Figure 3 – figure supplement 1.

(8) Merge Figures 6, 7, and 8 (or at least 7 and 8) to facilitate the comparison of data obtained with different proteins or conditions.  

We have merged Figures 7 and 8.

(9) Line 303: when referring to the chemical structure of sTCO-sulfo-Cy5, refer to Figure 4 Supp 1 and not Figure 9. Alternatively, consider moving Fig 9 to supplementary information or placing it earlier in the figure list.  

We now refer to the earlier supplemental figure when describing the structure of sTCO-sulfo-Cy5.

(10) Ensure proper referencing of Figure 4E in the text, particularly since it's vital to understanding the selection of mutation sites for the Insulin receptor, as discussed in lines 392-400. 

We have made this correction.

(11) Maintain citation consistency by verifying that all references cited in the text, including those in the Introduction, Results, and Discussion sections, are included in the References list at the end of the paper.

We have reviewed all our citations for consistency.

The reviewer is also concerned by the lack of any statistical analyses, and of appropriate control experiments:

(1) The trapping of PI3K at the plasma membrane, shown in Figure 3 supplementary 1, is not very convincing. It is unclear whether PI3K is trapped at the membrane, as claimed by the authors, or whether PI3K slowly accumulates at the membrane independently of the light stimulation. Indeed, the baseline fluorescence isn't flat to start with (especially in F-11 cells), and the change in fluorescence under 650 nm light is very modest, much weaker, in fact, than in control experiments without TRPV1 (Figure 2C). Do the authors observe a similar drift in fluorescence in absence of photostimulation at 650 nm? Such control experiment needs to be performed and discussed. More importantly, authors need to provide quantitative (and not just qualitative) measures of the changes in fluorescence observed in the different conditions, and run adequate statistical analyses to compare the different conditions (for all the figures of the manuscript where this applies).  

We can see that the language of “trapped at the membrane” is more of an interpretation than a description. We now describe this result as a lack of dissociation of PIF-iSH2 from the membrane in response to 750 nm light. We more clearly explain our interpretation and label it as speculative.

(2) Consider moving Figure 3 Supplementary 1 from supplementary information to the main document due to its importance. It seems like an important finding to me, and I believe also to the authors, who wrote a whole paragraph on PI3K trapping in the discussion section (lines 361-380).  

We agree that the results from this figure are important. To better align with the request of all reviewers to shorten the manuscript and reduce the number of figures in the main text, however, we have left the figure in the supplement.

(3) Figure 3: why is the increase in IP3 levels not reversible as in Figure 2? Is this because IP3 is detected only at the membrane level (TIRF experiment) and not the entire cell? Authors should comment on this aspect. 

As described in response to Comment#2, we now better explain our interpretation. Briefly, we speculate that the PIF-iSH2 that encounters TRPV1 in the plasma membrane binds to the ankyrin repeat domain of TRPV1 and, therefore, does not readily dissociate from membrane in response to 750 nm light.

(4) Figure 4E: Verify the functionality of the Insulin receptor mutants, as was done for TRPV1.  

We have added new experiments to demonstrate that the insulin receptor incorporating Tet3-Bu is functional. Because the insulin receptor is not electrogenic, we could not use electrophysiology to validate its function. Instead, we measured the insulin-dependent endocytosis of the receptor. These data are now presented in Figure 3 – figure supplement 2 and Figure 3 –  supplemental movie.

(5) Figures 6 to 8: The authors quantify the change in plasma membrane expression of TRPV1 and insulin receptors after NGF treatment (or photoactivation), but an important control experiment is missing. They first label cells with sulfo-Cy5, then treat them with NGF (or photoactivate them with 650 nm light), and then label them again with sulfo-Cy5, supposedly to label only the TRPV1 receptors that newly arrived at the membrane. However, we have no evidence that the first sulfo-Cy5 labeling (1 uM, 5 min) was complete. In fact, labeling with sulfo-Cy5 (200 nM) in Figure 4 never reaches saturation, not even after 20 min. The authors need to control for this, by comparing the change in fluorescence with and without NGF treatment. The GFP control is simply not sufficient. Also, include Figure 8 in the text, as it is missing from the results section, and discuss the results in more detail. Indeed, the current data is appealing as it suggests that what was observed with TRPV1 is also true for the Insulin receptor, but without a proper control this could just be an artefact.  

We have performed several new control experiments to address the reviewer’s concerns. (1) For NGF-induced increase in TRPV1 at the plasma membrane, we repeated the experiment using a vehicle instead of NGF. These data, added to Figure 4E, demonstrate that the increase in plasma membrane TRPV1 depends on NGF. (2) For the light-activated increase in plasma membrane TRPV1, we repeated the experiment using a second exposure to the deactivating 750 nm light instead of the activating 650 nm light and added the data as Figure 5, figure supplement 1A-E. These new data demonstrate that the increase in plasma membrane TRPV1 occurred only in response to  the activating wavelength of light. (3) To address the same as the previous comment, but for the insulin receptor, we repeated the insulin receptor experiments also using a second exposure to the deactivating wavelength of light. These data are now shown in Figure 5, figure supplement 1F-I and demonstrate that the increase in the insulin receptor levels in the plasma membrane required the activating wavelength of light.

(6) Line 313: "Importantly, sTCO-sulfo-Cy5 did not appear to equilibrate across the cell membrane and did not label untransfected cells (i.e., those without GFP; Figure 4 - figure supplement 1)". I don't see where the absence of labeling of untransfected cells is shown. The authors should show fluorescence changes on the surface of both transfected and untransfected cells and, as discussed above, quantify the data and provide statistical analyses.

See response to Reviewer #2, Comment #2.

Minor Comments:

(1) Define « PM » and « RTK » in abstract  We have made the requested changes.

(2) Consider presenting the signaling pathways defined in the introduction in a scheme to improve readability.  

We have added the signaling pathways defined in the introduction to Figure 1A.

(3) In Figure 1A, include the CAAX lipidation signal in the schematic representation.  

We had already shown the lipidation itself, but we have added the lipidation signal as a magenta star, with its meaning explained in the figure legend. We hope the reviewer finds this useful.

(4) Terminology clarification: Given the broad readership of Elife, provide clearer explanations for terms and techniques used, such as the function of PIF (line 144).  

We define the acronym PIF in the text, but do not further elaborate on the biological function of PIF to align with other reviewers’ requests that we reduce the review-type material in the manuscript.

(5) Correct "m-1s-1" to "M-1s-1" in line 119.  

This is now corrected.

(6) Replace "activate" with "activation" in line 122.  

This is now corrected.

(7) Indicate 650 nm and 750 nm next to the arrows in Figure 2B for reader clarity.  

We have added the requested arrow labels.

(8) Correct Figure 5A to Figure 4A in line 244.  

This is now corrected.

(9) Correct Figure 5B to Figure 5C in line 293.  

This is now corrected.

(10) In lines 274, 293, 312 and 329, clearly specify which panels of the referenced figures are being discussed to avoid confusion. 

We have now clearly specified which panels are being referenced.

(11) Figure 1B: it is unclear how long after 650 nm light switching the image is taken. The red bar indicating 650 nm light makes it look like the image is taken right after light switching, which would suggest that PIF-YFP trafficking to the membrane takes milliseconds in response to 650 nm light. However, the legend says that photoactivation kinetics are in the range of 10 seconds. Please accurately position the red bar in Figure 1B to reflect the time between light switching and imaging, and specify the time between light switching and imaging in the figure legend.  

We have more accurately shown the timing of image acquisition in what is now Figure 1, figure supplement 1.

(12) Please add a merged image for all the immune data figure.

We are uncertain about which figures the reviewer is referring to. We do not have any immunohistochemistry in the manuscript.  

(13) Line 205: "we found that expression of TRPV1 trapped PIF-iSH2 at the PM upon stimulation with 650 nm light, so that it no longer translocated to the cytoplasm in response to 750 nm light (Figure 3B and Figure 3 - figure supplement 1A)." This is shown in the supplementary figure but not in Figure 3B. Same issue with the following sentence.  

We have corrected the figure references in the text.

(14) For Figures 7 and 8, the authors state ""We next asked whether click chemistry labeling could be executed in cells in which we also used the PhyB/PIF machinery for activating PI3K." Is this really the main motivation for conducting these experiments?

Good point. We have improved the writing around this issue.

Author response:

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

eLife assessment

This important study identifies differential Orsay virus infection of C. elegans when animals are fed on different bacteria. The evidence for this is however, incomplete, as experiments to control for feeding rate and bacterial pathogenicity are needed as well as direct quantification of viral load. 

We appreciate that the editors and reviewers felt that our manuscript addressed an important problem. We appreciate the constructive critiques provided by the reviewers and have worked to address all of the concerns, including a number of additional experiments as indicated below.

Public Reviews:

Reviewer #1 (Public Review):

Summary: 

This manuscript explores the importance of food type on virus infection dynamics using a nematode virus as a model system. The authors demonstrate that susceptibility to viral infection can change by several orders of magnitude based on the type of bacterial food that potential hosts consume. They go on to show that, for the bacterial food source that reduces susceptibility, the effect is modulated by quorum sensing molecules that the bacteria produce. 

Strengths: 

This manuscript shows convincingly that nematode susceptibility to viral infection changes by several orders of magnitude (i.e. doses must be increased by several orders of magnitude to infect the same fraction of the population) depending on the bacterial food source on which hosts are reared. The authors then focus on the bacteria that reduce host susceptibility to viral infection and demonstrate that certain bacterial quorum-sensing compounds are required to see this effect of reduced susceptibility. Overall, sample sizes are large, methods are generally rigorous, experiments are repeated, and patterns are clear. 

Weaknesses: 

Although the molecular correlate of reduced susceptibility is identified (i.e. quorum sensing compounds) the mechanisms underlying this effect are missing. For example, there are changes in susceptibility due to altered nutrition, host condition, the microbiome, feeding rate, mortality of infected hosts, etc. In addition, the authors focus almost entirely on the reduction in susceptibility even though I personally find the increased susceptibility generated when reared on Ochrobactrum to be much more exciting. 

I was a bit surprised that there was no data on basic factors that could have led to reductions in susceptibility. In particular, data on feeding rates and mortality rates seem really important. I would expect that feeding rates are reduced in the presence of Pseudomonas. Reduced feeding rates would translate to lower consumed doses, and so even though the same concentration of virus is on a plate, it doesn't mean that the same quantity of virus is consumed. Likewise, if Pseudomonas is causing mortality of virus-infected hosts, it could give the impression of lower infection rates. Perhaps mortality rates are too small in the experimental setup to explain this pattern, but that isn't clear in the current version of the manuscript. Is mortality greatly impacted by knocking out quorum-sensing genes? Also, the authors explored susceptibility to infection, but completely ignored variation in virus shedding. 

We have added data on feeding rates (Line numbers 141-148 and 176-182, Supplementary Figure 4). After six hours of exposure no differences in feeding rate were observed. After 24 hours minor differences emerged between O. vermis MYb71 and each Pseudomonas species, however feeding rate inversely correlated with susceptibility to Orsay virus in that O. vermis MYb71 displayed the lowest feeding rate while P. aeruginosa PA14 displayed the highest feeding rate.

We have also added data on mortality rates (Line numbers 183-200, Supplementary Figure 6). No significant mortality was observed within the 24-hour exposure period used for our Orsay infection and transmission assays. P. aeruginosa virulence is dependent upon temperature and as our assays are done at 20°C rather than 25°C this may account for reduced mortality compared to other published results. Regardless, we noted that O. vermis MYb71 killed C. elegans as quickly as P. aeruginosa PA14 under these conditions and these two bacteria led to the shortest lifespan compared to the other tested bacteria. Interestingly, P. lurida MYb11 was observed to be more virulent than P. aeruginosa PA01 under these conditions. These results suggest that there is no direct correlation between mortality and susceptibility to Orsay virus, although it does not rule out that virulence effects unique to each bacterium could contribute to alterations in host susceptibility.  

The reviewer is correct to assert that differences in viral shedding could exist. However, our susceptibility assays using exogenous Orsay virus remove this source of variation and yet we still observe the same trends such that O. vermis MYb71 promotes infection while P. lurida MYb11, P. aeruginosa PA01, and P. aeruginosa PA14 attenuate infection. Further we measured the amount of virus shed into the lawns in the presence of different bacteria and did not observe differences in shed virus that could account for the differences we observe in incidence proportion (Line numbers 241-254, Fig. 3 F). Viral stability could be an issue in both the transmission and susceptibility assays. We therefore tested viral stability in the presence of E. coli, P. lurida MYb11, P. aeruginosa PA01, and P. aeruginosa PA14 and successfully recovered virus from all lawns, suggesting virus is not rapidly degraded in the presence of any bacterium (Fig. 3D and 3E). However, we noted that the recovery of Orsay virus from lawns of E. coli OP50 and P. lurida MYb11 within 30 minutes was decreased compared to a spike-in control suggesting recovery from each lawn is not equivalent. This complicates a comparison of viral stability and shedding rates between different bacteria, but our ability to recover substantial amounts of virus in the shedding assay from the three Pseudomonas strains we examined precludes a substantial decrease in shedding rates as an explanation for the robust attenuation of Orsay virus observed in transmission assays.  

I was also curious why the authors did not further explore the mechanism behind the quorumsensing effect. Not sure whether this is possible, but would it be possible to add spent media to the infection plates where the spent media was from Pseudomonas that produce the quorum sensing compound but the plates contain OP50, Pseudomonas, or the quorum sensing knockout of Pseudomonas? That would reveal whether it is the compound itself vs. something that the compound does. 

We observed that quorum sensing mutants suppressed the attenuation of Orsay virus infection and we agree that this could be a consequence of the compounds themselves, or more likely an effect of the downstream consequences of quorum signaling. We added culture supernatant from each bacterium to lawns of E. coli OP50 to assess the effect on host susceptibility and did not observe any potent effect (Line numbers 311-318, Supplementary Figure 9). This supports an interpretation that it is not the compound itself that is responsible, however we cannot rule out that the compounds themselves may be responsible if provided at a higher concentration.

In addition, I was surprised by how much focus there was on the attenuation of infection and how little there was on the enhancement of infection. To me, enhancement seems like the more obvious thing to find a mechanism for -- is the bacteria suppressing immunity, preventing entry to gut cells, etc? 

We are also intrigued by the enhancement of infection by Ochrobactrum spp, however we chose to focus on attenuation given the availability of Pseudomonas aeruginosa genetic mutants for study. We have added data (Line numbers 371-402, Figure 7, and Supplemental Figure 12) that inform our current hypothesis regarding Ochrobactrum mediated enhancement of Orsay virus infection.

I was a bit concerned about the "arbitrary units", which were used without any effort to normalize them. David Wang and Hongbing Jiang have developed a method based on tissue culture infectious dose 50 (TCID50) that can be used to measure infectious doses in a somewhat repeatable way. Without some type of normalization, it is hard to imagine how this study could be repeated. The 24-hour time period between exposure and glowing suggests very high doses, but it is still unclear precisely how high. Also, it is clear that multiple batches of virus were used in this study, but it is entirely unclear how variable these batches were. 

We have clarified that we also measured the (TC)ID50 for every batch of virus used similar to the methods suggested by the Wang laboratory (Line numbers 107-119 and 499-506). We have added a figure showing the virus batch variability for all batches used in this study (Supp. Fig. 2). We have further clarified that the arbitrary units correspond to the actual microliters of viral filtrate used during infection and provided clear methods to replicate our viral batch production to assist with issues of reproducibility (Line numbers 107-119 and 499-506).

The authors in several places discuss high variability or low variability in incidence as though it is a feature of the virus or a feature of the host. It isn't. For infection data (or any type of binomial data) results are highly variable in the middle (close to 50% infection) and lowly variable at the ends (close to 0% or 100% infection). This is a result that is derived from a binomial distribution and it should not be taken as evidence that the bacteria or the host affect randomness. If you were to conduct dose-response experiments, on any of your bacterial food source treatments, you would find that variability is lowest at the extremely high and extremely low doses and it is most variable in the middle when you are at doses where about 50% of hosts are infected. 

Thank you for pointing this out, we have removed all reference to this throughout the manuscript.

Reviewer #2 (Public Review):

Summary and Major Findings/Strengths:

Across diverse hosts, microbiota can influence viral infection and transmission. C. elegans is naturally infected by the Orsay virus, which infects intestinal cells and is transmitted via the fecal-oral route. Previous work has demonstrated that host immune defense pathways, such as antiviral RNAi and the intracellular pathogen response (IPR), can influence host susceptibility to virus infection. However, little is known about how bacteria modulate viral transmission and host susceptibility. 

In this study, the authors investigate how diverse bacterial species influence Orsay virus transmission and host susceptibility in C. elegans. When C. elegans is grown in the presence of two Ochrobactrum species, the authors find that animals exhibit increased viral transmission, as measured by the increased proportion of newly infected worms (relative to growth on E. coli OP50). The presence of the two Ochrobactrum species also resulted in increased host susceptibility to the virus, which is reflected by the increased fraction of infected animals following exposure to the exogenous Orsay virus. In contrast, the presence of Pseudomonas lurida MYb11, as well as Pseudomonas PA01 or PA14, attenuates viral transmission and host susceptibility relative to E. coli OP50. For growth in the presence of P. aeruginosa PA01 and PA14, the attenuated transmission and susceptibility are suppressed by mutations in regulators of quorum sensing and the gacA two-component system. The authors also identify six virulence genes in P. aeruginosa PA14 that modulate host susceptibility to virus and viral transmission, albeit to a lesser extent. Based on the findings in P. aeruginosa, the authors further demonstrate that deletion of the gacA ortholog in P. lurida results in loss of the attenuation of viral transmission and host susceptibility. 

Taken together, these findings provide important insights into the species-specific effects that bacteria can have on viral infection in C. elegans. The authors also describe a role for Pseudomonas quorum sensing and virulence genes in influencing viral transmission and host susceptibility. 

Major weaknesses: 

The manuscript has several issues that need to be addressed, such as insufficient rigor of the experiments performed and questions about the reproducibility of the data presented in some places. In addition, confounding variables complicate the interpretations that can be made from the authors' findings and weaken some of the conclusions that are stated in the manuscript. 

(1) The authors sometimes use pals-5p::GFP expression to indicate infection, however, this is not necessarily an accurate measure of the infection rate. Specifically, in Figures 4-6, the authors should include measurements of viral RNA, either by FISH staining or qRT-PCR, to support the claims related to differences in infection rate. 

Following the reviewers comment we have corroborated our pals-5::GFP data using FISH staining (Line numbers 291-292 and 357-359, Figure 4D & 4E, and Figure 6C).  

(2) In several instances, the experimental setup and presentation of data lack sufficient rigor. For example, Fig 1D and Fig 2B only display data from one experimental replicate. The authors should include information from all 3 experimental replicates for more transparency. In Fig 3B, the authors should include a control that demonstrates how RNA1 levels change in the presence of E. coli OP50 for comparison with the results showing replication in the presence of PA14. In order to support the claim that "P. aeruginosa and P. lurida MYb11 do not eliminate Orsay virus infection", the authors should also measure RNA1 fold change in the presence of PA01 and P. lurida in the context of exogenous Orsay virus. Additionally, the authors should standardize the amount of bacteria added to the plate and specify how this was done in the Methods, as differing concentrations of bacteria could be the reason for species-specific effects on infection. 

All experimental replicates are now included within the supplementary information. 

We have also measured RNA1 fold change following infection in the presence of P. aeruginosa PA01 and P. lurida MYb11 (Line numbers Fig 3B and 3C) and found that these bacteria also do not eliminate Orsay virus replication. 

We thank the reviewer for their comment on controlling the amount of bacteria and have clarified our methods section to more clearly explain that we seed our plates with equivalent amounts (based on volume) of overnight bacterial culture before allowing the bacteria to grow on the plates for 48 hours.  

(3) The authors should be more careful about conclusions that are made from experiments involving PA14, which is a P. aeruginosa strain (isolated from humans), that can rapidly kill C. elegans. To eliminate confounding factors that are introduced by the pathogenicity of PA14, the authors should address how PA14 affects the health of the worms in their assays. For example, the authors should perform bead-feeding assays to demonstrate that feeding rates are unaffected when worms are grown in the presence of PA14. Because Orsay virus infection occurs through feeding, a decrease in C. elegans feeding rates can influence the outcome of viral infection. The authors should also address whether or not the presence of PA14 affects the stability of viral particles because that could be another trivial reason for the attenuation of viral infection that occurs in the presence of PA14. 

We have added data on feeding rates (Line numbers 141-148 and 176-182, Supplementary Figure 4). After six hours of exposure no differences in feeding rate were observed. After 24 hours minor differences emerged between O. vermis MYb71 and each Pseudomonas species, however feeding rate inversely correlated with susceptibility to Orsay virus in that O. vermis MYb71 displayed the lowest feeding rate while P. aeruginosa PA14 displayed the highest feeding rate.

We have also added data on mortality rates (Line numbers 183-200, Supplementary Figure 6). No significant mortality was observed within the 24-hour exposure period used for our Orsay infection and transmission assays. P. aeruginosa virulence is dependent upon temperature and as our assays are done at 20°C rather than 25°C this may account for reduced mortality compared to other published results. Regardless, we noted that O. vermis MYb71 killed C. elegans as quickly as P. aeruginosa PA14 under these conditions and these two bacteria led to the shortest lifespan compared to the other tested bacteria. Interestingly, P. lurida MYb11 was observed to be more virulent than P. aeruginosa PA01 under these conditions. These results suggest that there is no direct correlation between mortality and susceptibility to Orsay virus, although it does not rule out that virulence effects unique to each bacterium could contribute to alterations in host susceptibility.  

We tested viral stability in the presence of E. coli OP50 and Pseudomonas spp. and successfully recovered virus from all lawns, suggesting virus is not rapidly degraded in the presence of P. lurida MYb11, P. aeruginosa PA01, and P. aeruginosa PA14 (Line numbers 241-249, Fig 3D and Fig 3E). However, we noted that the recovery of Orsay virus from lawns of E. coli OP50 and P. lurida MYb11 within 30 minutes was decreased compared to a spike-in control suggesting recovery from each lawn is not equivalent. This complicates a comparison of viral stability and shedding rates between different bacteria, but our ability to recover substantial amounts of virus in the shedding assay from each Pseudomonas species precludes a substantial decrease in shedding rates as an explanation for the robust attenuation of Orsay virus observed in transmission assays.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Overall, I really liked this manuscript, I do think there are areas for improvement though. 

Some smaller things: 

Line 84: "can be observed spreading from a single animal" -- this isn't really great wording because the virus itself can't be observed (at least not very easily) -- even infection is hard to see. 

The wording in line 84-85 has now been adjusted to read “can spread from a single animal”.

Fig 1C: which groups are statistically significantly different from each other? 

Statistics have now been added to Figure 1C. 

Line 154: not necessary to do for this paper, but this sentence made me curious whether the effect would have been seen with mixtures of bacteria (i.e. what if 50% were OP50 and 50% were Pseudomonas?) 

This data has now been added in Line numbers 372-378, Figure 7A, and Supp. Fig. 12A and 12B.

Line 262-264: I don't find this interesting at all for the reasons mentioned earlier about binomial data being the most variable in the middle. 

These lines have been removed.

Figure 4 B: The labels for the first two tick marks on the x-axis are switched I suspect. Otherwise, the controls did not behave as expected. 

Figure 4B has been corrected.

Line 288, 297 and several other places: "Orsay Virus" should be "Orsay virus". 

We have corrected these instances.

Supplemental Figure 2: Labels in the figure legend are B and C instead of A and B. 

These labels have been adjusted for their placement within Figure 6.

Line 411: I suspect this was supposed to be 13,200 xg rather than 13.2 xg. 

This error has been corrected.

Line 416-417: This sentence is very hard to interpret. More details are needed. This is the ID50 in which host strain? Is this averaged over all batches of virus? How variable are the batches? 

This sentence (line number 114) has been amended to clarify that all ID50 values referred to here were calculated for ZD2611 populations in the presence of E. coli OP50. Further, Supplementary Figure 2 now shows all the ID50 values measured for each batch of virus used in this manuscript resulting in an average ID50 of 3.6.

Lines 467-469: Why exclude these instead of counting them as zeros in the analysis? How many plates fit this description -- were there lots or only a few over the course of all experiments? 

We have chosen to exclude these plates as these samples lost spreaders at some point during the course of the assay potentially skewing the eventual number of new infections counted depending on when the infected spreader animal crawled off the plate.  We have detailed the number of plates that fit this description in lines 559-562. 

Line 476: A critical detail that is missing here is what number of worms were counted to score infection. Please say here or in the figure legends. 

We have added the total number of worms counted and the minimum number counted per plate for each assay in the figure legends.

Line 546: Why was only a single representative experiment shown? I'm asking for a justification, not necessarily for you to show all the data. 

We chose to show a single representative experiment for two reasons:  We noted variability between susceptibility assays even when using the same batch of virus such that we could not combine experiments into a single plot as we did for transmission assays. Second, while we could normalize to a control within each experiment and expect to see similar relative differences across experiments, we believe this makes it more difficult to interpret the underlying data. For example, an increase in the infection rate of 80% compared to 10% within a population has only a single interpretation while a relative increase in the infection rate by 8x within a population could have several underlying meanings (e.g. 80% vs 10%, 64%vs 8%, 24% vs 3%). We have now included all experimental replicates in the supplementary material. 

Reviewer #2 (Recommendations For The Authors):

Minor concerns: 

(1) Lines 86-87: "utilized a collection of bacteria isolated from the environment with wild C. elegans". The authors should provide more context on the source of these bacterial strains. 

More references for the sources of these bacteria have been added to Supplementary Table 2.

(2) The presentation of data in Fig 1 could be improved. The authors should include the text "pals-5p::GFP" on the images shown in Fig 1B. The red dashed line in Fig. 1D should intersect the dose-response curve at y = 0.5. The column heading for Fig 1E states "ID50 +/- SD (a.u.)", but should read "ID50 ratio" and should not have units. It also might be more intuitive to normalize the ID50 value for O. vermis to E. coli OP50. This way, having an ID50 ratio >1 indicates decreased transmission relative to E. coli, and ID50 ratio <1 indicates increased transmission relative to E. coli. To increase the transparency and rigor of 1E, the authors should plot the ratios from all 3 experimental replicates. The authors should also briefly explain why different viral doses were used in Fig 1D and 1F. 

The text “pals-5p::GFP” has now been added to Figure 1B and throughout the text. The red dashed line in figure 1D has been corrected. Figure 1E has been adjusted to an actual figure as suggested and the y-axis label is “ID50 Ratio Compared to E. coli OP50”. The ID50 replicates have been plotted in Supplementary Figure 2. We have clarified that the doses used are the same. Briefly, the technical replicates of individual doses from Figure 1D and Supplementary Figure 3A and 3B were pooled and processed for FISH staining to provide each experimental replicate of Figure 1F. 

(3) Line 110: The claim is that Ochrobactrum and P. lurida MYb11 reduce the variability of infection levels. However, another possibility is that there's simply less dynamic range in the assay because the infection levels have been compressed to 100% and 0% under these conditions. 

This line has been removed.

(4) There are discrepancies between what is shown in Fig 2C and what is described in the text. Lines 163-164: "P. aeruginosa PA01 and P. lurida MYb11 attenuated average infection to 33% and 62% of the population respectively". In Fig 2C, the mean for PA01 is ~25% whereas the mean for P. lurida appears to be less than 62%. 

These values have been corrected.

(5) Line 196: Provide more context for why rde-1 mutants were tested. This is the first time rde-1 is mentioned in the text (i.e. why show results in rde-1 mutants when the results are in Fig 2). 

More context has been provided for why rde-1 mutants were tested (Line numbers 228-232). Briefly, using the rde-1 mutant, which has defective antiviral immunity and therefore supports higher viral replication levels than the wild-type (Félix et al. 2011), allows us to potentiate our infection assay in Figure 3B and 3C such that we maximize our chances of detecting viral replication in the presence of the Pseudomonas species, and especially P. aeruginiosa PA14, where fewer animals might be expected to get infected based upon Figure 2B and Supplementary Figure 5. 

(6) Lines 228-229: "Mutations of any the regulators of the las, rhl, or pqs quorum sensing systems suppressed the attenuation of Orsay virus infection caused by the presence of wild-type P. aeruginosa PA01". Based on this description, PA01 should have a lower fraction of GFP positive relative to the quorum sensing mutants in Fig 4B. It seems that the x-axis labels OP50 and PA01 are swapped. 

The x-axis labels of Figure 4B have been corrected. 

(7) To improve clarity, for any figures that have data showing the "fraction of individuals GFP positive", the authors should include "pals-5p::GFP" in the y-axis title and legend. 

The y-axis labels, legends, and text have been corrected throughout.  

(8) To improve overall clarity and flow, the order in which the data is presented could be reordered. In particular, Fig. 6 could be better positioned instead of being the last figure, as no further characterization is performed on the mutants, and the findings are not conserved in strains that are more relevant to the C. elegans microbiota, such as P. lurida. The overall story could be strengthened if the authors ended the manuscript with more details related to the mechanism by which regulators of quorum sensing modulate the outcome of viral infection. 

Figure 5 and Figure 6 have now been swapped.

(9) Fig 5A: Make arrow sizes consistent across diagrams (i.e. the diagram for gacA deletion). 

This figure (now Figure 6A) has been adjusted to make arrow sizes consistent across diagrams.  

(10) Lines 280-282: "These data suggest that gacA has a conserved role across distant Pseudomonas species..." Here, the authors can provide more context on how well-conserved gacA is across Pseudomonas species (i.e. phylogenetic analysis of gacA sequences across different Pseudomonas species/strains). Furthermore, the data in Fig 5 does not provide strong enough support for the conclusion that gacA has a conserved role broadly across Pseudomonas species, as the authors only assess the effects of a gacA deletion in two species, P. aeruginosa and P. lurida. 

We have adjusted lines 361-362 to “These data suggest that gacA has a conserved role between P. aeruginosa and P. lurida Myb11 in the attenuation of Orsay virus transmission and infection of C. elegans.” to reflect that we only assessed the effects of the gacA deletion in P. aeruginosa and P. lurida MYb11.

(11) The manuscript can be strengthened by performing additional experiments to elucidate the mechanism by which Pseudomonas modulates viral infection. Does the attenuation of viral transmission and host susceptibility by P. lurida and P. aeruginosa require C. elegans to be in the presence of live bacteria? For example, the authors could measure viral transmission and susceptibility of C. elegans grown on heat-killed Pseudomonas. Additionally, it would be interesting to determine if modulation of viral infection is dependent on a secreted molecule. To assess this, the authors could perform viral infections in the context of Pseudomonas culture supernatant. 

We added bacterial culture supernatant from each bacterium to lawns of E. coli OP50 to assess the effect on host susceptibility and did not observe any potent effect (Line numbers 311-318, Supplementary Figure 9). This supports an interpretation that attenuation is not mediated by a secreted molecule, however we cannot rule out that attenuation activity would become apparent if supernatant were provided at a higher concentration.

We have found substantial challenges appropriately controlling live vs. heat-killed experiments particularly with the specifics of our susceptibility experiments. With regards to the underlying question of mechanism we believe that the genetic mutants (e.g. rhlR/gacA) are equally informative and that further comparison of these mutants’ interaction with the C. elegans host as compared to wild-type may be informative. 

(12) The authors should include a discussion on the relative virulence potential of PA01, PA14, and P. lurida and the relationship between bacterial virulence potential and the outcome of viral infection. 

We have also added data on mortality rates (Line numbers 183-200, Supplementary Figure 6). No significant mortality was observed within the 24-hour exposure period used for our Orsay infection and transmission assays. P. aeruginosa virulence is dependent upon temperature and as our assays are done at 20°C rather than 25°C this may account for reduced mortality compared to other published results. Regardless, we noted that O. vermis MYb71 killed C. elegans as quickly as P. aeruginosa PA14 under these conditions and these two bacteria led to the shortest lifespan compared to the other tested bacteria. Interestingly, P. lurida MYb11 was observed to be more virulent than P. aeruginosa PA01 under these conditions. These results suggest that there is no direct correlation between mortality and susceptibility to Orsay virus, although it does not rule out that virulence effects unique to each bacterium could contribute to alterations in host susceptibility.  

(13) More information is needed on strains listed in Supplementary Table 2, particularly when there is no reference listed and the strain is "Gift of XXX lab". For example, the Troemel lab previously published about an Ochrobactrum strain in Troemel et al PLOS Biology 2008 PMID: 19071962 - is this the same strain? Please ensure that there is adequate information about each strain with as many published references as possible so that the work can be more easily reproduced. 

We have added additional information and references to the strain table in Supplementary Table 2. The strain listed as Ochrobactrum sp. has been amended to Ochrobactrum BH3 as it is the strain described in Troemel et al. 2008.